# Summary of findings [Explanations]

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Summary of findings 2 Methods to decrease blood loss during liver resection (serious adverse events)

Summary of findings 3 Methods to decrease blood loss during liver resection (blood transfusion proportion)

# Background

## Description of the condition

Liver resection refers to removal of part of the liver. On average, 1800 liver resections are carried out in the UK (HES 2011), and 11,000 in the USA (Asiyanbola 2008), every year. In the western world, the main indication for liver resection is colorectal liver metastases. Colorectal cancer is the third most common cancer in the world. Approximately 1.2 million people develop colorectal cancer each year (IARC 2010), and 50% to 60% will have colorectal liver metastases (Garden 2006). Liver resection, the only curative option for people with colorectal liver metastases, is indicated in 20% to 30% of people in whom the metastasis is confined to the liver (Garden 2006). Five-year survival for people with colorectal liver metastases who undergo liver resection is about 40% (Garden 2006).

The second most common reason for liver resection is hepatocellular carcinoma. Hepatocellular carcinoma is one of the most common cancers, with a worldwide annual incidence of 750,000 people (IARC 2010). Most hepatocellular carcinomas develop in cirrhotic livers (Llovet 2005). Liver resection and liver transplantation are the main curative treatments (Llovet 2005; Taefi 2013). Of people who present with hepatocellular carcinoma, about 5% are suitable for liver resection (Chen 2006). Survival after surgery depends on the stage of cancer and the severity of the underlying chronic liver disease. People with early-stage disease (cancers smaller than 5 cm) have a five-year survival of about 50%, whereas people with more advanced disease have a five-year survival of about 30% (Chen 2006). Screening programmes in theory should lead to a diagnosis at an earlier stage, when surgery is feasible and is associated with better outcomes.

Liver resection may also be performed for benign liver tumours (Belghiti 1993). The liver is subdivided into eight Couinaud segments (Couinaud 1999), which can be removed individually or by right hemi-hepatectomy (Couinaud segments 5 to 8), left hemi-hepatectomy (segments 2 to 4), right trisectionectomy (segments 4 to 8), or left trisectionectomy (segments 2 to 5 and 8 ± 1) (Strasberg 2000). Although every liver resection is considered major surgery, only resection of three or more segments is considered a major liver resection (Belghiti 1993).

Blood loss during liver resection is an important factor affecting complications and mortality in people undergoing liver resection (Shimada 1998; Yoshimura 2004; Ibrahim 2006). Variable estimates of blood loss, ranging from 200 mL to 2 L, have been reported (Gurusamy 2009a). Major blood loss during surgery or in the immediate postoperative period may result in death of the patient. Major blood loss can be defined based on the Advanced Trauma Life Support (ATLS definition of class 3 or class 4 shock, where there is a loss of 30% or more of blood volume) (ATLS 2008). During liver resection, the liver parenchyma is transected at the plane of resection. The blood vessels and the bile duct branches in the plane of resection (cut surface) are then sealed by different methods to prevent blood or bile leakage.

## Description of the intervention

Various interventions have been attempted to decrease blood loss during liver resection. These interventions include temporary occlusion of the blood vessels that supply the liver (Gurusamy 2009a; Table 1); different methods of liver transection (the way that the liver parenchyma is divided), such as the clamp-crush method, the Cavitron ultrasonic surgical aspirator, or the radiofrequency dissecting sealer (Gurusamy 2009b; Table 2); and different methods of management of the cut surface of the liver (the way that the resection plane of the remnant liver is managed), such as use of fibrin sealant, argon beamer, or electrocautery and suture material (Frilling 2005; Table 3).

Interventions selected to decrease blood loss can be used alone or in various combinations ( Table 4). Usually surgeons at different centres follow their own protocol for decreasing blood loss. The finger-fracture and clamp-crush techniques do not involve specialist equipment. The minimum and standard method of managing the cut surface involves electrocautery and suture material. Altogether, the goal of these interventions is to decrease blood loss and the associated morbidity and mortality.

## How the intervention might work

Temporarily occluding the blood vessels that supply the liver may reduce the blood flow through the cut vessels. Different methods of liver transection are used to remove the liver parenchyma, so that damage to the blood vessels is minimized. This might result in clear visualisation of the blood vessels, which can be clamped and then divided. Different topical methods of managing the cut surface attempt to seal the blood vessels on the resection plane, preventing blood loss.

## Why it is important to do this review

Liver resection is a major surgical procedure with significant mortality (estimated at 4%) and morbidity (estimated at 40%) (Reissfelder 2011). Interventions that decrease blood loss may improve outcomes of liver resection. Each category of interventions has been systematically reviewed previously (Gurusamy 2009a; Gurusamy 2009b). However, to our knowledge, no review has been conducted to assess and synthesise the comparative effectiveness of specific combinations of interventions when used together to decrease blood loss and associated morbidity and mortality. This systematic review is intended as a useful guide for patients and healthcare providers as they seek to understand the role of different combinations of interventions (treatment strategies) in decreasing blood loss and blood transfusion requirements in people undergoing elective liver resection.

# Objectives

To assess the comparative benefits and harms of different treatment strategies that aim to decrease blood loss during elective liver resection.

# Methods

## Criteria for considering studies for this review

### Types of studies

We considered only randomised clinical trials for this overview. We excluded studies of other design.

### Types of participants

We included randomised clinical trials in which participants underwent elective liver resection using different types of vascular occlusion or no vascular occlusion, irrespective of the method of vascular occlusion or the nature of the background liver (i.e., normal or cirrhotic), different types of parenchymal transection, or different types of management of cut surface. We excluded randomised clinical trials in which participants underwent liver resection combined with other major surgical procedures (e.g., one-stage liver and bowel resection for synchronous metastases from colorectal tumours).

### Types of interventions

We included randomised clinical trials that assessed one or more of the following interventions in this review.

- Methods of vascular occlusion (including no vascular occlusion).
- Methods of liver parenchymal transection.
- Methods of management of the cut surface (resection plane) of the liver.

The surgeon (and hence the trialists) may use a particular combination of each of the above. For example, one surgeon may perform liver resection using intermittent vascular occlusion, clamp-crush technique as the method of liver parenchymal transection, and a fibrin sealant on the cut surface; while another surgeon may perform liver resection without using any method of vascular occlusion, with the Cavitron ultrasonic surgical aspirator as the method of liver parenchymal transection, and without any fibrin sealant on the cut surface. Each combination was assessed as a treatment strategy, that is, a combination of several interventions. The purpose of this review was to identify the overall treatment effect of a treatment strategy rather than the contribution of each component intervention towards the overall effect.

Commonly used surgical techniques under each of the above categories are listed in Table 1, Table 2, and Table 3. In practice, any intervention in Table 1 can be used in combination with an intervention from Table 2 or Table 3. Any intervention in Table 2 can be used in combination with an intervention from Table 3. However, because of the few trials that could be included for network meta-analysis (sparse data) in this review, we revised the categories of vascular occlusion, method of parenchymal transection, and dealing with the cut surface to those shown in Table 4.

### Types of outcome measures

We assessed the comparative effectiveness of available treatment strategies that aimed to decrease blood loss during liver resection for the following outcomes.

#### Primary outcomes

- Mortality.
- Short-term (30-day mortality or in-hospital mortality). We used in-hospital mortality as defined in the included trials.
- Long-term (at maximal follow-up).

- Serious adverse events. An adverse event was defined as any untoward medical occurrence not necessarily having a causal relationship with the treatment but resulting in a dose reduction or discontinuation of treatment (ICH-GCP 1997). A serious adverse event was defined as any event that would increase mortality; was life-threatening; required inpatient hospitalisation; or resulted in persistent or significant disability; or any important medical event that might have jeopardised the person or required intervention to prevent it. Serious adverse events correspond approximately to Grade III or above of the Clavien-Dindo classification - the only validated system for classifying postoperative complications (Dindo 2004; Clavien 2009; Table 5). In cases where the authors did not classify the severity of adverse events, we followed the criteria provided in Table 5 to classify the severity.
- Quality of life as defined in the included trials.
- Short-term (30 days, three months).
- Long-term (maximal follow-up).

#### Secondary outcomes

- Blood transfusion requirements.
- Number of participants who required red cell or whole blood heterologous blood transfusion.
- Quantity of blood transfusion (heterologous red cell or whole blood product, platelet, and fresh frozen plasma).
- Total operative blood loss.
- Number of participants who had major operative blood loss.

- Hospital stay.
- Length of total hospital stay (including re-admissions).
- Intensive therapy unit stay.

- Operating time.
- Time needed to return to work.

## Search methods for identification of studies

### Electronic searches

We searched the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, and Science Citation Index Expanded (Royle 2003) to 16 July 2012. We also searched the World Health Organization International Clinical Trials Registry Platform search portal, which searches various trial registers, including ISRCTN and ClinicalTrials.gov (apps.who.int/trialsearch/Default.aspx) to identify further trials. Because subsets of all available interventions on this topic have been reviewed comprehensively in existing Cochrane systematic reviews (Gurusamy 2009a; Gurusamy 2009b), we also used these reviews as a way to identify trials. Search strategies with time spans of the searches are available in Appendix 1.

### Searching other resources

We searched the references of the identified trials to identify additional trials for inclusion.

## Data collection and analysis

### Selection of studies

Two review authors (CS and JV) independently identified the trials for inclusion by screening the titles and abstracts. We sought full text for any references that were identified for potential inclusion by at least one of the authors. We made further selection for inclusion based on the full text. We have listed the full texts of references that we excluded with reasons for the exclusion (Characteristics of excluded studies table). We planned to list any ongoing trials identified primarily through World Health Organization International Clinical Trials Registry Platform for further follow-up. We resolved discrepancies through discussion.

### Data extraction and management

Two review authors (CS and JV) independently extracted the following data.

- Year and language of publication.
- Country in which the participants were recruited.
- Year(s) in which the trial was conducted.
- Inclusion and exclusion criteria.
- Participant characteristics such as age, sex, underlying disease, comorbidity, number and proportion of participants with cirrhosis, and number and proportion of participants undergoing major versus minor liver resection.
- Details of the intervention and treatment strategy that aimed to decrease blood loss and blood transfusion requirements (e.g., surgical technique, procedure and co-intervention, concurrent surgery, and medications).
- Follow-up time points.
- Risk of bias (Assessment of risk of bias in included studies).

We sought unclear or missing information by contacting the authors of the individual trials. If there was any doubt whether trials shared the same participants - completely or partially (by identifying common authors and centres) - we planned to contact the authors of the trials to clarify whether the trial report was duplicated. We resolved any differences in opinion through discussion.

### Assessment of risk of bias in included studies

We followed the guidance given in the Cochrane Handbook for Systematic Reviews of Intervention (Higgins 2011), and those described in the Cochrane Hepato-Biliary Group Module (Gluud 2013), to assess the risk of bias in included studies. Specifically, we assessed the risk of bias in included trials for the following domains (Schulz 1995; Moher 1998; Kjaergard 2001; Wood 2008; Lundh 2012; Savovic 2012a; Savovic 2012b).

#### Allocation sequence generation

- Low risk of bias: sequence generation was achieved using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice were adequate if performed by an independent adjudicator.
- Uncertain risk of bias: the trial was described as randomised, but the method of sequence generation was not specified.
- High risk of bias: the sequence generation method was not, or may not have been, random. Quasi-randomised studies (those using dates, names, or admittance numbers to allocate participants) were inadequate and were excluded for the assessment of benefits but not for assessing harms.

#### Allocation concealment

- Low risk of bias: allocation was controlled by a central and independent randomisation unit, sequentially numbered, opaque and sealed envelopes, or something similar, so that intervention allocations could not have been foreseen in advance of, or during, enrolment.
- Uncertain risk of bias: 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.
- High risk of bias: if the allocation sequence was known to the investigators who assigned participants, or the study was quasi-randomised. Quasi-randomised studies were excluded for assessment of benefits but not for assessment of harms.

#### Blinding of participants and personnel

- Low risk of bias: blinding was performed adequately, or the outcome measurement was not likely to be influenced by lack of blinding.
- Uncertain risk of bias: information was insufficient to allow assessment of whether the type of blinding used was likely to induce bias on the estimate of effect.
- High risk of bias: no blinding or incomplete blinding and the outcome or the outcome measurements were likely to be influenced by lack of blinding.

#### Blinding of outcome assessors

- Low risk of bias: blinding was performed adequately, or the outcome measurement was not likely to be influenced by lack of blinding.
- Uncertain risk of bias: information was insufficient to allow assessment of whether the type of blinding used was likely to induce bias on the estimate of effect.
- High risk of bias: no blinding or incomplete blinding and the outcome or the outcome measurements were likely to be influenced by lack of blinding.

#### Incomplete outcome data

- Low risk of bias: the underlying reasons for missing data were unlikely to make treatment effects depart from plausible values, or proper methods have been employed to handle missing data.
- Uncertain risk of bias: information was insufficient to allow assessment of whether the missing data mechanism in combination with the method used to handle missing data was likely to induce bias on the estimate of effect.
- High risk of bias: the crude estimate of effects (e.g., complete case estimate) were clearly biased because of the underlying reasons for missing data, and the methods used to handle missing data were unsatisfactory.

#### Selective outcome reporting

- Low risk of bias: pre-defined or clinically relevant and reasonably expected outcomes (mortality and serious adverse events) were reported.
- Uncertain risk of bias: not all pre-defined or clinically relevant and reasonably expected outcomes were reported, or they were not reported fully, or it was unclear whether data on these outcomes were recorded.
- High risk of bias: one or more clinically relevant and reasonably expected outcomes were not reported; data on these outcomes were likely to have been recorded.

#### Vested interest bias

- Low risk of bias: the trial was conducted by a party with no vested interests (i.e., a party benefiting from the results of the trial) in the outcome of the trial.
- Uncertain risk of bias: It was not clear if the trial was conducted by a party with vested interest in the outcome of the trial.
- High risk of bias: the trial was conducted by a party with vested interests in the outcome of the trial (such as a drug manufacturer).

We considered a trial at low risk of bias if the trial was assessed as at low risk of bias for all domains. We considered a trial at low risk of bias for an outcome if the trial was assessed as at low risk of bias for all study level domains, as well as for outcome-specific domains (e.g., blinding, incomplete outcome data). Otherwise, trials with uncertain risk of bias or with high risk of bias regarding one or more domains were considered trials with high risk of bias.

### Measures of treatment effect

For dichotomous variables (short-term mortality, serious adverse events, participants requiring blood transfusion), we calculated the odds ratio (OR) with 95% credible interval (CrI). For continuous variables, such as quantity of blood transfused, blood loss, hospital stay, and operating time, we calculated the mean difference (MD) with 95% CrI. We planned to use MD and 95% CrI for time needed to return to work but did not use this since none of the included trials reported this outcome. We planned to use standardised mean difference (SMD) with 95% CrI for quality of life if different scales were used (but did not plan to combine the quality of life at different time points) and for the quantity of blood transfused (some authors report this in litres transfused, while others report this as number of units transfused). For time-to-event data, such as long-term survival, we planned to use hazard ratio (HR) with 95% CrI.

We have also presented the 'Summary of findings' tables using GRADEpro (ims.cochrane.org/revman/other-resources/gradepro) for each outcome.

### Unit of analysis issues

The unit of analysis were the people undergoing elective liver resection according to the intervention group to which they were randomly assigned.

### Dealing with missing data

We performed an intention-to-treat analysis (Newell 1992), whenever possible. Otherwise, we used data that were available to us (e.g., a trial may have reported only per-protocol analysis results). As such 'per protocol' analyses may be biased, we planned to conduct best-worst case scenario and worst-best case scenario analyses as sensitivity analyses.

For continuous outcomes, we imputed the standard deviation from P values according to guidance given in the Cochrane Handbook for Systematic Reviews of Intervention (Higgins 2011). If the data were likely to be normally distributed, we used the median for meta-analysis when the mean was not available. If it was not possible to calculate the standard deviation from the P value or the confidence intervals, we imputed the standard deviation using the largest standard deviation in other trials for that outcome. This form of imputation may decrease the weight of the study for calculation of mean differences and may bias the effect estimate to no effect for calculation of SMDs (Higgins 2011).

### Assessment of heterogeneity

We assessed clinical and methodological heterogeneity by carefully examining the characteristics and design of included trials. Major sources of clinical heterogeneity included cirrhotic compared to non-cirrhotic livers and major compared to minor liver resections. In addition, we anticipated considerable heterogeneity in the way the intervention was performed. For example, intermittent portal triad clamping may be performed with different time periods of occlusion and non-occlusion. In addition, different doses of fibrin sealant may be used. Different study design and risk of bias may contribute to methodological heterogeneity.

We used the residual deviance and Deviance Information Criteria (DIC) for assessing between study heterogeneity as per the guidance from the National Institute for Health and Care Excellence (NICE) Decision Support Unit (DSU) Technical Support Documents (Dias 2012b; Dias 2013). We also calculated the between-trial standard deviation and have reported this if we used a random-effects model. See Data synthesis for further details regarding residual deviance, DIC, and choice of model.

If substantial heterogeneity was identified - clinical, methodological, or statistical - we planned to explore and address heterogeneity in a subgroup analysis (see section on Subgroup analysis and investigation of heterogeneity).

### Assessment of reporting biases

We planned to use visual asymmetry on a funnel plot to explore reporting bias in case at least 10 trials were included for direct comparison (Egger 1997; Macaskill 2001). In the presence of heterogeneity that could be explained by subgroup analysis, we planned to perform the funnel plot for each subgroup in the presence of the adequate number of trials. We planned to perform the linear regression approach described by Egger 1997 to determine the funnel plot asymmetry. However, these were not performed because of the lack of an adequate number of trials.

We also considered selective reporting as evidence of reporting bias.

### Data synthesis

We planned to apply classifications described in Table 1, Table 2, and Table 3 to categorise different methods of vascular occlusion and parenchymal transection, as well as methods used to manage the cut surface of the liver. Each category in the table is broadly defined to encompass a relatively homogeneous group of interventions, although we anticipate that variations will be noted in the way each method is carried out. For example, intermittent portal triad clamping may be performed with different time periods of occlusion and non-occlusion. We categorised them under intermittent portal triad clamping regardless of the time intervals. Likewise, we did not distinguish different maximum periods for continuous vascular occlusion (Clavien 1996), and did not determine whether the suprahepatic inferior vena cava or the hepatic veins were occluded for outflow obstruction. These practice variations might be a source of heterogeneity; however, evidence was insufficient to suggest that these variations may affect the outcome.

In liver resection, a surgeon typically uses one item from Table 1, one item from Table 2, and one item from Table 3. Together, one can consider this combination of one method from each table as a treatment strategy, or in terms of network meta-analysis, each unique treatment strategy can be defined as a 'node'. Because of the large number of possible treatment strategies (eight methods of vascular occlusion × six methods of parenchymal transection × four methods of treatment of cut surface, i.e., 192 potential treatment strategies or nodes), we planned to construct a more sparse network graph based on treatment strategies used in the trials that we identified. We did not expect that all 192 nodes would be represented in the trials available in the literature. However, since the data were sparse, we categorised the treatments into fewer categories by having only three methods of vascular occlusion (no vascular occlusion, continuous vascular occlusion, or intermittent vascular occlusion) and by having only two methods of treatment of cut surface (fibrin sealant used or no fibrin sealant used) ( Table 4) as indicated in the protocol. This reduced the categories to 36 treatment strategies or nodes (three methods of vascular occlusion × six methods of parenchymal transection × two methods of treatment of cut surface).

We did not anticipate that every node would be represented. Some methods are more commonly practiced than others. From Table 1, no vascular occlusion, intermittent portal triad clamping, and continuous portal triad clamping are used more often than other techniques (Gurusamy 2009a). From Table 2, clamp-crush method and Cavitron ultrasonic surgical aspirator are more commonly applied (Gurusamy 2009b). The clamp-crush method and the finger-fracture method do not require any special equipment, but the remaining methods do require special equipment. From Table 3, common methods of managing cut surface include suturing for large and medium vessels and ducts and performing electrocauterisation of small vessels and ducts (Gurusamy 2009b).

#### Direct comparison

We planned to perform pair-wise meta-analyses using Review Manager 5 (RevMan 2012), in accordance with recommendations of The Cochrane Collaboration (Higgins 2011), and those described in the Cochrane Hepato-Biliary Group Module (Gluud 2013). We planned to use both random-effects models (DerSimonian 1986) and fixed-effect models (DeMets 1987) for the meta-analyses. In case of discrepancy between the two models, we planned to report the results of both; otherwise, we planned to report results of the random-effects model. We planned to use the generic inverse method to combine the HRs for time-to-event outcome data.

We did not perform direct comparisons. This was because of the exclusion of many trials that might have been suitable for direct comparison but were unsuitable for the overview. Although these trials included comparisons of one aspect of different methods of vascular occlusion or parenchymal transection or management of cut surface, one or more aspects of methods of vascular occlusion or parenchymal transection or management of cut surface not being compared were either not stated or were chosen in a non-random manner. Therefore, these trials had to be excluded for this review while such trials would be eligible for inclusion in a direct comparison involving only one aspect of methods of vascular occlusion or parenchymal transection or management of cut surface. For example, a trial comparing vascular occlusion versus no vascular occlusion provided details on the method of vascular occlusion ( Table 1) but may not provide details of the parenchymal dissection ( Table 2) or the method of dealing with cut surface ( Table 3). Since the objective of this review was to assess the overall effect of the different components and not to assess the effect of each individual component, we excluded such trials. Performing and reporting the direct comparison after excluding such trials may not provide the same effect estimate as that obtained if such trials were included. Stakeholders interested in the effects of the individual components should refer to the reviews where the objectives were to assess the benefits and harms of individual components (Gurusamy 2009a; Gurusamy 2009b).

#### Network meta-analysis

We conducted network meta-analyses to compare multiple interventions simultaneously for each of the outcomes, primary outcomes and one secondary outcome on blood transfusion requirements. Network meta-analysis combines direct evidence within trials and indirect evidence across trials (Mills 2012).

We obtained a network plot to ensure that the trials were connected by treatments using Stata/IC 11 (StataCorp LP). We excluded any trials that were not connected to the network. We conducted a Bayesian network meta-analysis using the Markov chain Monte Carlo method in WinBUGS 1.4. We modelled the treatment contrast (e.g., log OR for binary outcomes, MD for continuous outcomes) for any two interventions ('functional parameters') as a function of comparisons between each individual intervention and an arbitrarily selected reference group ('basic parameters') (Lu 2004). The reference group was selected on the basis of the 'least intervention', for example, if a treatment group had no vascular occlusion, used finger-fracture or clamp-crush method for parenchymal transection, and no fibrin sealant for dealing with the cut surface, this treatment was used as the reference category. We performed the network analysis as per the guidance from The NICE DSU documents (Dias 2013). Further details of the codes used, the raw data, and the technical details of how we performed the analysis are shown in Appendix 2, Appendix 3, and Appendix 4. The codes allow handling of trials with multiple arms to be dealt in the same way as two-arm trials, that is, one can enter the data from all the arms in a trial as number of events and the number of people exposed to the event for binary outcomes or the mean and standard error for continuous outcomes. The choice of the model between fixed-effect model and random-effects model was based on the model fit as per the guidelines of the NICE TSU (Dias 2013). We have reported the treatment contrasts (i.e., log ORs for binary outcomes and MDs for continuous outcomes) of the different treatments in relation to the reference treatment, the deviance residuals, number of effective parameters, and DIC for fixed-effect model and random-effects model for each outcome. We have also reported the parameters used to assess the model fit (i.e., deviance residuals, number of effective parameters, and DIC) for the inconsistency model for all the outcomes where there was evidence from direct and indirect comparisons. We have reported estimates of treatment effects (ORs for binary outcomes and MDs for continuous outcomes). The 95% CrIs are calculated in the Bayesian meta-analysis, which is similar in use to the 95% confidence intervals in the frequentist meta-analysis. We have calculated the 95% CrI from the mean and variance and have reported the effect estimates and associated 95% CrI for each pair-wise comparison in a table. We have also estimated the probability that each intervention ranks at one of the possible positions. We have presented the probability that a treatment ranks as the best treatment in graphs. It should be noted that a less than 90% probability that the treatment is the best treatment is unreliable (Dias 2012a). We have also presented the cumulative probability of the treatment ranks (i.e., the probability that the treatment is within the top two, the probability that the treatment is within the top three, etc.) in graphs. We have also plotted the probability that each treatment is best for each of the different outcomes (rankogram), which are generally considered more informative (Salanti 2011; Dias 2012a).

#### Sample size calculations

To control for the risk of random errors, we interpreted the information with caution when the accrued sample size in the meta-analysis was less than the required sample size (required information size). For calculation of the required information size, please see Appendix 5.

### Subgroup analysis and investigation of heterogeneity

We planned to perform the following subgroup analyses when at least one trial was included in each subgroup.

- Trials with low risk of bias compared to trials with high risk of bias.
- Cirrhotic compared to non-cirrhotic livers.
- Major liver resections compared to minor liver resections.

We planned to use the Chi^{2} test to identify subgroup differences. We planned to consider a P value < 0.05 as statistically significant. We also planned to use meta-regression to assess the impact of cirrhotic versus non-cirrhotic livers and major versus minor liver resections on effect estimates in the presence of at least 10 trials with this information.

We did not perform any of the above because of the few trials included in this network meta-analysis.

### Sensitivity analysis

Reporting of the severity of adverse events may be inadequate or incomplete. For example, minor bile leaks are considered mild adverse events, and major bile leaks are considered serious adverse events. In cases where the severity could not be determined, we planned to exclude those events from the main analysis. We planned to perform a sensitivity analysis to include those events and treat them as severe adverse events in the sensitivity analysis. We did not perform this since we were able to assess the severity of the reported complications.

# Results

## Description of studies

### Results of the search

We identified 1347 references through electronic searches of CENTRAL (N =170), MEDLINE (N = 370), EMBASE (N = 442), Science Citation Index Expanded (N = 364), and randomised controlled trials registers (N = 1). We excluded 494 duplicates and 768 clearly irrelevant references through screening titles and reading abstracts. We retrieved 85 references for further assessment. No references were identified through scanning reference lists of the identified randomised trials. We excluded 76 references (73 studies) for the reasons listed under the table Characteristics of excluded studies. In total, nine references of nine completed randomised clinical trials met the inclusion criteria (Belghiti 1999; Capussotti 2003; Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011; Park 2012). This is summarised in the study flow diagram (Figure 1).

Figure 1. Study flow diagram. |

### Included studies

The treatments used in the nine randomised clinical trials have been summarised in Characteristics of included studies table and in Table 6. All the trials assessed different methods of open liver resection by using different combinations of vascular exclusion, parenchymal transection, and management of the liver cut surface, in order to decrease blood loss during liver resection. Seven trials were two-arm trials (Belghiti 1999; Capussotti 2003; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Park 2012). There was one three-arm trial (Doklestic 2011), and one four-arm trial (Lesurtel 2005). However, one arm in each of these trials was excluded since the method of parenchymal transections used in these trials (parenchymal transection using bipolar cautery and water jet) were not included in this review (Lesurtel 2005; Doklestic 2011). Eleven different treatments out of 36 possible treatments were included in the studies included in this review. A total of 617 participants were randomised to the 11 different treatments in these trials. However, four treatment strategies in two trials were not connected to the network in any of the outcomes (Belghiti 1999; Capussotti 2003). Thus, we included 496 participants randomised to seven different treatment strategies in the seven trials that contributed data for the network meta-analysis (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011; Park 2012).

### Excluded studies

Of the 73 studies excluded, 24 studies were excluded because they were not randomised clinical trials (Taniguchi 1992; Shimada 1994; Rau 1995; Johnson 1998; Cherqui 1999; Man 2002; Smyrniotis 2002; Smyrniotis 2003; Chau 2005; Nagano 2005; Noritomi 2005; Sugo 2005; Aldrighetti 2006; Felekouras 2006; Wu 2006; Chiappa 2007; Kim 2007; Xia 2008; Cresswell 2009; Fu 2010; Pietsch 2010; Wang 2011; Palibrk 2012; Yokoo 2012). One report was the protocol of a trial (Rahbari 2009). Seven trials did not compare different methods of vascular occlusion or parenchymal transection or method of management of cut surface (Lentschener 1997; Hasegawa 2002; Matot 2002; Yao 2006; Hashimoto 2007; Kato 2008; Guo 2010). One trial included participants undergoing liver resection along with other major procedures (Figueras 2007). Four trials compared variations of methods of vascular occlusion that would have been classified under the same treatment categories included in this review (Wu 2002; Chen 2006a; Fu 2011; Van Den Broek 2011). The remaining 36 trials included comparisons of one aspect of different methods of vascular occlusion or parenchymal transection or management of cut surface. However, one or more aspects of methods of vascular occlusion or parenchymal transection or management of cut surface not being compared were either not stated or were chosen in a non-random manner. Therefore, we have excluded these trials (Kohno 1992; Belghiti 1996; Noun 1996; Man 1997; Chapman 2000; Takayama 2001; Figueras 2003; Man 2003; Wong 2003; Chouker 2004; El-Kharboutly 2004; Schwartz 2004; Arita 2005; Figueras 2005; Frilling 2005; Koo 2005; Lodge 2005; Esaki 2006; Saiura 2006; Wang 2006; Campagnacci 2007; Chapman 2007; Izzo 2008; Kim 2008; Schmidt 2008; El-Moghazy 2009; Ikeda 2009; Liang 2009; Richter 2009; Dello 2011; Fischer 2011; Gugenheim 2011; Mirza 2011; Rahbari 2011; Scatton 2011; Capussotti 2012).

## Risk of bias in included studies

The risk of bias in the included trials is summarised in Figure 2 and Figure 3. All trials were at high risk of bias.

Figure 2. Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies. |

Figure 3. Risk of bias summary: review authors' judgements about each risk of bias item for each included study. |

### Allocation

Four trials (44%) had adequate sequence generation (Capussotti 2003; Capussotti 2006; Lupo 2007; Park 2012). Two trials (22%) had adequate allocation concealment (Petrowsky 2006; Doklestic 2011). Thus, no trials (0%) had low risk of bias due to allocation.

### Blinding

None of the trials reported any blinding.

### Incomplete outcome data

Eight of the nine trials (89%) were free from bias due to incomplete outcome data (Belghiti 1999; Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011; Park 2012).

### Selective reporting

Seven trials (78%) reported mortality and serious adverse events and hence were considered to be free from bias (Belghiti 1999; Capussotti 2003; Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007).

### Other potential sources of bias

Only one trial reported the source of funding and we rated the vested interest bias to be low in this trial (Doklestic 2011). The remaining trials were at unclear risk of bias.

## Effects of interventions

See: Summary of findings for the main comparison Methods to decrease blood loss during liver resection (mortality); Summary of findings 2 Methods to decrease blood loss during liver resection (serious adverse events); Summary of findings 3 Methods to decrease blood loss during liver resection (blood transfusion proportion)

All the data used for analysis are provided in Appendix 3. Analyses in this section were based on the 496 participants in the seven trials that contributed data for the network meta-analysis (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011; Park 2012).

### Mortality

All the seven trials (496 participants) provided data for the network meta-analysis on short-term mortality (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011; Park 2012). There were seven deaths in the included studies giving an overall mortality of 1.4%. The network plot is shown in Figure 4. Although there is no need to add an arbitrary constant of 0.5 to each of the cells for occasional zero-event trials when the meta-analysis is performed using the Bayesian methods (Dias 2013), we had to add this arbitrary constant in our meta-analysis since many of the trials had no deaths reported.

Figure 4. Network plot of mortality Treatment codes are provided in Table 6. |

The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 7. The between-study standard deviation (tau) was 0.60. As indicated in Table 7, the fixed-effect model was preferred based on the DIC statistics. There was no evidence of inconsistency in the network. The pair-wise ORs for the different treatment comparisons are shown in Table 8. As shown in Table 8, there is no evidence of any significant difference in mortality between the different treatments. The absolute proportion of people with mortality based on an illustrative risk of 3.5% (Finch 2007) is shown in Summary of findings for the main comparison. As shown in Figure 5, none of the treatments ranked best with more than 90% probability. As shown in Figure 6, there is substantial uncertainty about the treatment strategy with lowest mortality.

Figure 5. Mortality - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 6. Mortality - cumulative probability of ranks of different treatments There is more than 90% probability that IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin) is within the five best treatments (of seven treatments). All the remaining treatments other than ContVascSharpNoFib (continuous vascular occlusion with sharp dissection and no fibrin) are within the six best treatments. This suggests that there is substantial uncertainty about the treatment with least mortality. Treatment codes are provided in Table 6. |

None of the trials reported long-term mortality.

### Serious adverse events

Five trials (406 participants) provided data for the network meta-analysis on serious adverse events (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007). There were 35 people with serious adverse events in the included studies (8.6%). The network plot is shown in Figure 7. The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 9. The between-study standard deviation (tau) was 0.03. As indicated in Table 9, the fixed-effect model was preferred based on the DIC statistics. There was no evidence of inconsistency in the network. The pair-wise ORs for the different treatment comparisons is shown in Table 8. As shown in Table 10, there was no evidence of any significant difference between the different treatments except for a significant increase in the proportion of people with serious adverse events in the NoVascRFAblNoFib (no vascular occlusion with radiofrequency dissecting sealer and no fibrin) compared with NoVascClampNoFib (no vascular occlusion with clamp-crush and no fibrin) (OR 7.13; 95% CrI 1.77 to 28.65). The absolute proportion of people with serious adverse events based on an illustrative risk of 6.7% in the reference treatment is shown in Summary of findings 2. As shown in Figure 8, none of the treatments ranked best with more than 90% probability. As shown in Figure 9, there is a high probability that NoVascClampNoFib (no vascular occlusion with clamp-crush method and no fibrin) and IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasonic surgical aspirator (CUSA) and no fibrin) are better than other treatments with regards to serious adverse events.

Figure 7. Network plot of serious adverse events Treatment codes are provided in Table 6. |

Figure 8. Serious adverse events - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 9. Serious adverse events - cumulative probability of ranks of different treatments There is more than 90% probability that NoVascClampNoFib (no vascular occlusion with clamp-crush method and no fibrin) and IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin) are within the three best treatments (of seven treatments). This suggests that there is a high probability that these two treatments are better than other treatments with regards to serious adverse events. Treatment codes are provided in Table 6. |

### Quality of life

None of the trials reported quality of life.

### Blood transfusion requirements

#### Proportion transfused

Six trials (446 participants) provided data for the network meta-analysis on proportion of people transfused (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Lupo 2007; Doklestic 2011). The network plot is shown in Figure 10. The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 11. As indicated in Table 11, the random-effects model was preferred based on the DIC statistics. The between-study standard deviation (tau) was 0.61. There was no evidence of inconsistency in the network. The pair-wise ORs for the different treatment comparisons are shown in Table 12. As shown in Table 12, there is no evidence of any significant difference in the proportion of people transfused between the different treatments. The absolute proportion of people requiring blood transfusion based on an illustrative risk of 15.7% in the reference treatment is shown in Summary of findings 2. As shown in Figure 11, none of the treatments ranked best with more than 90% probability. As shown in Figure 12, there was substantial uncertainty about the treatment with lowest proportion of people transfused.

Figure 10. Network plot of blood transfusion proportion Treatment codes are provided in Table 6. |

Figure 11. Blood transfusion - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 12. Blood transfusion proportion - cumulative probability of ranks of different treatments There is more than 90% probability that ContVascClampNoFib (continuous vascular occlusion with clamp-crush and no fibrin) is within the five best treatments (of seven treatments) and that NoVascClampNoFib (no vascular occlusion with clamp-crush and no fibrin) is within the six best treatments (of seven treatments). This suggests that there is substantial uncertainty about the treatment with proportion of people with blood transfusion. Treatment codes are provided in Table 6. |

#### Quantity of blood transfused

Two trials (155 participants) provided data for the network meta-analysis on quantity of blood transfused (Smyrniotis 2005; Petrowsky 2006). The network plot is shown in Figure 13. The results and model-fit of the fixed-effect model and random-effects model is provided in Table 13. The between-study standard deviation (tau) was 0. As indicated in Table 13, the fixed-effect model was preferred based on the DIC statistics. We have not reported the model-fit of the inconsistency model since there was no closed loop in the network. The pair-wise MDs for the different treatment comparisons are shown in Table 14. As shown in Table 14, people undergoing liver resection by IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) had significantly higher amounts of blood transfused than people undergoing liver resection by ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) (MD 1.2 units; 95% CrI 0.08 to 2.32). There were no significant differences in the other comparisons. As shown in Figure 14, none of the treatments ranked best with more than 90% probability. As shown in Figure 15, there was a high probability that ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) and ContVascSharpNoFib (continuous vascular occlusion with sharp dissection and no fibrin) are better than IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) with regards to quantity of blood transfused.

Figure 13. Network plot of quantity of blood transfused Treatment codes are provided in Table 6. |

Figure 14. Quantity of blood transfusion - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 15. Quantity of blood transfused - cumulative probability of ranks of different treatments There is more than 90% probability that ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) and ContVascSharpNoFib (continuous vascular occlusion with sharp dissection and no fibrin) are within the two best treatments. This suggests that these two treatments are better than IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) with regards to the quantity of blood transfused. Treatment codes are provided in Table 6. |

#### Operative blood loss

Three trials (281 participants) provided data for the network meta-analysis on operative blood loss (Smyrniotis 2005; Capussotti 2006; Petrowsky 2006). The network plot is shown in Figure 16. The results and model-fit of the fixed-effect model and random-effects model is provided in Table 15. The between-study standard deviation (tau) was 0.02. As indicated in Table 15, the fixed-effect model was preferred based on the DIC statistics. We have not reported the model-fit of the inconsistency model since there was no closed loop in the network. The pair-wise mean differences for the different treatment comparisons are shown in Table 16. As shown in Table 16, people undergoing liver resection by ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) had significantly lower blood loss than those undergoing liver resection by NoVascClampNoFib (no vascular occlusion with clamp-crush method and no fibrin) (MD -130.9 mL; 95% CrI -255.89 to -5.91). There were no significant differences in the other comparisons. As shown in Figure 17 and Figure 18, ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) was ranked the best treatment with regards to operative blood loss with more than 90% probability.

Figure 16. Network plot of operative blood loss Treatment codes are provided in Table 6. |

Figure 17. Operative blood loss - best treatment There is a more than 90% probability that ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin) is the best treatment. Treatment codes are provided in Table 6. |

Figure 18. Operative blood loss - cumulative probability of ranks of different treatments There is more than 95% probability that ContVascClampNoFib (continuous vascular occlusion with clamp-crush and no fibrin) is within the two best treatments. This suggests that there is little uncertainty about the treatment with least operative blood loss. Treatment codes are provided in Table 6. |

#### Major blood loss

None of the trials included in the network meta-analysis reported the proportion of people who developed major blood loss (class 3 or class 4 shock according to ATLS definition) (ATLS 2008). In one trial, two participants in the ContVascSharpNoFib (continuous vascular occlusion with sharp dissection and no fibrin sealant) were re-operated due to significant post-operative bleeding (Smyrniotis 2005). The authors stated that this was related to the sharp dissection method of parenchymal transection (Smyrniotis 2005). In another trial, one participant in NoVascCUSANoFib (no vascular occlusion with CUSA and no fibrin sealant) underwent re-operation for significant post-operative bleeding (Park 2012).

### Hospital stay

#### Length of hospital stay

Six trials (446 participants) provided data for the network meta-analysis on length of hospital stay (Lesurtel 2005; Smyrniotis 2005; Capussotti 2006; Petrowsky 2006; Doklestic 2011; Park 2012). The network plot is shown in Figure 19. The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 17. The between study standard deviation (tau) was 0.01. As indicated in Table 17, the fixed-effect model was preferred based on the DIC statistics. There was no evidence of inconsistency in the network. The pair wise mean differences for the different treatment comparisons is shown in Table 18. As shown in Table 18, there is no evidence of any significant difference in the length of hospital stay between the different treatments. As shown in Figure 20, none of the treatments ranked best with more than 90% probability. As shown in Figure 21, there is substantial uncertainty about the treatment with least length of hospital stay.

Figure 19. Network plot of length of hospital stay Treatment codes are provided in Table 6. |

Figure 20. Length of hospital stay - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 21. Length of hospital stay - cumulative probability of ranks of different treatments There is more than 90% probability that IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin) is within the four best treatments (of seven treatments). NoVascClampNoFib (no vascular occlusion with clamp-crush and no fibrin) and ContVascClampNoFib (continuous vascular occlusion with clamp-crush and no fibrin) are within the five best treatments. This suggests that there is substantial uncertainty about the treatment with least length of hospital stay. Treatment codes are provided in Table 6. |

#### Intensive therapy unit stay

Four trials (261 participants) provided data for the network meta-analysis on intensive therapy unit stay (Lesurtel 2005; Smyrniotis 2005; Petrowsky 2006; Doklestic 2011). The network plot is shown in Figure 22. The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 19. The between-study standard deviation (tau) was 0. As indicated in Table 19, the fixed-effect model was preferred based on the DIC statistics. There was no evidence of inconsistency in the network. The pair-wise MDs for the different treatment comparisons are shown in Table 20. As shown in Table 20, there is no evidence of any significant difference in intensive therapy unit stay between the different treatments. As shown in Figure 23, none of the treatments ranked best with more than 90% probability. As shown in Figure 24, IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin) was within the three best treatments (of six treatments) and IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) may be better than other treatments with regards to intensive therapy unit stay with a high probability.

Figure 22. Network plot of intensive therapy unit stay Treatment codes are provided in Table 6. |

Figure 23. Intensive therapy unit (ITU) stay - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 24. Intensive therapy unit (ITU) stay - cumulative probability of ranks of different treatments There is more than 90% probability that IntVascCUSANoFib (intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin) is within the three best treatments (of six treatments). IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) is within the four best treatments with a more than 90% probability. This suggests that these two treatments may be better than other treatments with regards to ITU stay. Treatment codes are provided in Table 6. |

### Operating time

Four trials (245 participants) provided data for the network meta-analysis on operating time (Lesurtel 2005; Smyrniotis 2005; Petrowsky 2006; Park 2012). The network plot is shown in Figure 25. The results and model-fit of the fixed-effect model and random-effects model along with the model-fit of the inconsistency model is provided in Table 21. The between-study standard deviation (tau) was 0.01. As indicated in Table 21, the fixed-effect model was preferred based on the DIC statistics. We have not reported the model-fit of the inconsistency model since there was no closed loop in the network. The pair-wise MDs for the different treatment comparisons are shown in Table 22. As shown in Table 18, people undergoing liver resection by IntVascCUSANoFib method (intermittent vascular occlusion with CUSA and no fibrin) had significantly longer operating time than people undergoing liver resection by NoVascCUSANoFib (no vascular occlusion with CUSA and no fibrin) (MD 49.61 minutes; 95% CrI 29.81 to 69.41). There is no evidence of any significant difference in the operating time between the other comparisons. As shown in Figure 26, none of the treatments ranked best with more than 90% probability. As shown in Figure 27, there is substantial uncertainty about the treatment with least operating time.

Figure 25. Network plot of operating time Treatment codes are provided in Table 6. |

Figure 26. Operating time - best treatment None of the treatments are considered to be the best treatment since the probabilities did not reach 90% or above. Treatment codes are provided in Table 6. |

Figure 27. Operating time - cumulative probability of ranks of different treatments There is more than 90% probability that NoVascCUSANoFib (no vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin), ContVascClampNoFib (continuous vascular occlusion with clamp-crush method and no fibrin), and IntVascClampNoFib (intermittent vascular occlusion with clamp-crush method and no fibrin) are within the four best treatments (of five treatments). This suggests that there is substantial uncertainty about the treatment with least operating time. Treatment codes are provided in Table 6. |

### Time needed to return to work

None of the trials reported the time needed to return to work.

### Overall results

As shown in Figure 28, none of the treatments appear clearly superior to others when all the outcomes are considered together. We did not give any specific weighting to the different outcomes. However, if serious adverse events are considered more important than all the outcomes other mortality, NoVascClampNoFib (no vascular occlusion with clamp-crush method and no fibrin) and IntVascCUSANoFib (intermittent vascular occlusion with CUSA and no fibrin) are better than other treatments with regards to serious adverse events. NoVascRFAblNoFib (no vascular occlusion with radiofrequency dissecting sealer and no fibrin) appears to be the worst in terms of serious adverse events. There does not seem to be much correlation between a treatment being best in reducing blood transfusion and being best in reducing serious adverse events and mortality.

Figure 28. Rankogram This shows the probability that the treatment is best for each outcome. None of the treatments appear clearly superior to others when all the outcomes are considered together. There does not seem to be much correlation between a treatment being best in reducing blood transfusion and being best in reducing serious adverse events and mortality. Treatment codes are provided in Table 6. |

### Subgroup analysis

Subgroup analysis was not performed because of the paucity of data.

# Discussion

## Summary of main results

This is the first network meta-analysis comparing different techniques aimed at decreasing blood loss during liver resection. Overall, there does not seem to be any major advantage of one combination of techniques over another. Mortality was generally low in all the groups compared to that reported in previous studies (Finch 2007). This may be because of the careful selection of participants included in randomised clinical trials compared to a consecutive case series where the results of all liver resections were reported. We have provided the sample size calculations based on a mortality of 3.5% observed in consecutive series (Finch 2007). To achieve a 20% relative reduction in mortality (20% relative risk reduction) from 3.5% to 2.8%, more than 20,000 participants are required for a single direct comparison to demonstrate a significant reduction in mortality with a specific intervention. As shown in the Methods section, the effective sample size in an indirect comparison involving just three treatments is only a fraction of the number of participants included in the trials. An example is shown in the Methods section where 10,000 participants included in the indirect comparisons is equivalent to fewer than 2000 participants in the absence of heterogeneity and fewer than 1000 participants in the presence of moderate heterogeneity. Even without these complicated calculations, one can easily observe from the credible intervals that the credible intervals were very wide ( Summary of findings for the main comparison; Table 7). This means that we cannot rule out a significant benefit or harm by using different treatments. Given the number of participants required to show a significant benefit of treatment with relation to mortality and serious adverse events, trials of this magnitude are unlikely to be funded. The serious adverse events were significantly higher with radiofrequency dissecting sealer compared with clamp-crush method in the absence of vascular occlusion or use of fibrin. There was no significant difference between the other groups. There was a high probability that 'no vascular occlusion with clamp-crush method and no fibrin' and 'intermittent vascular occlusion with Cavitron ultrasound surgical aspirator and no fibrin' were better than other treatments with regards to serious adverse events. However, based on wide credible intervals, there is considerable uncertainty about the benefit of these methods over the methods other than radiofrequency dissecting sealer. In addition, there is no corroborative evidence in the form of these treatments reducing intensive therapy unit stay or length of hospital stay, which would be anticipated if an intervention made a significant reduction in serious adverse events.

None of the trials reported quality of life, which is an important outcome used in assessing the cost-effectiveness of a treatment in a state-funded healthcare system. Given that the quality of life would depend upon various factors including peri-operative complications, length of hospital stay, and time to return to work, it is likely to be easier to demonstrate a significant difference in quality of life if the treatment was effective than to demonstrate a difference in mortality or serious adverse events. Future randomised clinical trials should use a validated quality of life measure.

The major purpose of different methods of liver resection is to decrease the blood loss and blood transfusion requirements. As mentioned in the Background, various methods have been attempted to achieve this. Some methods do not require any additional equipment (e.g., vascular occlusion), while other methods require special equipment (e.g., Cavitron ultrasonic surgical aspirator or radiofrequency dissecting sealer). There was no significant difference in the proportion of people who underwent blood transfusion dependent on the technique utilised. Parenchymal transection by clamp-crush method with continuous vascular occlusion resulted in significantly lower blood loss than parenchymal transection by clamp-crush method with no vascular occlusion and significantly lower quantity of blood transfused than parenchymal transection by clamp-crush method with intermittent vascular occlusion. However, the reduction in blood loss and quantity of blood transfused was modest. It should also be noted that ischaemic preconditioning (temporary occlusion of vessels supplying the liver to 'condition' the liver to blood flow occlusion before exposing the liver to a prolonged period of blood flow occlusion) was used prior to continuous vascular occlusion with a maximum continuous clamp period of 75 minutes in one trial (Petrowsky 2006), and in the other trial, ischaemic preconditioning was used in the second half of the trial (Smyrniotis 2005). Therefore, caution is needed in interpreting these results and in applying the results in people without ischaemic preconditioning. In addition, this must be put into context. Serious adverse events are likely to result in decreased quality of life for patients and increased costs to the healthcare provider and are, therefore, more important endpoints than a modest decrease in blood transfusion.

There was no significant difference in the hospital stay or intensive therapy unit stay. These are important to the patients, their carers, and the healthcare funders. None of the trials reported time taken to return to work, which is an important outcome for the patient and their carers in the absence of significant sickness benefit and is an important outcome for the healthcare provider in a state-funded healthcare system with significant sickness benefits.

Thus overall, there is no current evidence to prefer one treatment over another. Simple methods such as clamp-crush method do not appear to result in poorer outcomes than other methods that require special equipment. However, there is significant uncertainty on this topic.

## Overall completeness and applicability of evidence

The participants included in this trial underwent elective open liver resection and were generally anaesthetically fit. The findings of this review are applicable only to such patients.

## Quality of the evidence

The overall quality of evidence was very low. The risk of bias was high in all the trials. Using appropriate methods of randomisation and reporting the method of randomisation adequately will decrease selection bias. While healthcare providers (surgeons who performs the surgery) cannot be blinded to the treatments, it is possible to blind the surgeons who are involved in the day-to-day postoperative management of the patient. While it may be difficult to blind the anaesthetist to the treatment groups, using objective criteria for transfusion (NHS Blood and Transplant 2007), may overcome the problem of bias due to lack of blinding with regards to intra-operative blood transfusion. The intensivist involved in the post-operative care of the patient can be easily blinded. Objective criteria for detection of complications along with the postoperative management of the patient by a healthcare team not involved in the operation can decrease detection and performance bias. With regards to drop-outs, randomising the participants after confirming that the tumour can be removed can avoid post-randomisation drop-outs due to metastatic spread identified at the time of laparotomy. This can decrease attrition bias. Reporting all the important clinical outcomes can decrease selective reporting bias. There was no significant heterogeneity in all the outcomes other than proportion of blood transfused as indicated by the good model-fit achieved by fixed-effect model as compared to the random-effects model.

The effect estimates were wide with the credible intervals overlapping 1 and with either 20% reduction (0.80) or 20% increase (1.20) which can be considered a clinically significant effect. Future trials should be adequately powered to decrease the risk of random errors.

## Potential biases in the review process

We selected a range of databases without any language restrictions and conducted the meta-analysis according to the NICE TSU (Dias 2012a; Dias 2012b; Dias 2012c; Dias 2013). These are the strengths of the review process.

We have excluded studies because the methods of vascular occlusion, parenchymal transection, or method of management of the cut surface were not reported (Characteristics of excluded studies). Some of these studies may meet the inclusion criteria and may have contributed additional information. We imputed the standard deviation when they were not available from the trials. This may have resulted in a change in the effect estimates.

## Agreements and disagreements with other studies or reviews

This is the first network meta-analysis. Previously, we have compared individual components and concluded that intermittent vascular occlusion may decrease blood loss (Gurusamy 2009a), and that the clamp-crush method may decrease blood loss (Gurusamy 2009b). In this review, we have concluded that there is no evidence for any significant advantage of different methods of liver resection. The differences in conclusion may be because of the exclusion of trials in which the methods were not reported or when the other aspects of liver resection other than the component being compared were chosen in a non-random manner.

# Authors' conclusions

Implications for practice Very low quality evidence suggests that liver resection using a radiofrequency dissecting sealer without vascular occlusion or fibrin sealant may increase serious adverse events and this should be evaluated in further randomised clinical trials. The risk of serious adverse events with liver resection using no special equipment compared to more complex methods requiring special equipment is uncertain due to the very low quality of the evidence. The credible intervals were wide and considerable benefit or harm with a specific method of liver resection cannot be ruled out. |

Implications for research Trials need to be conducted and reported according to the SPIRIT (Standard Protocol Items: Recommendations for Interventional Trials) statement (www.spirit-statement.org/) and the CONSORT (Consolidated Standards for Reporting of Trials) statement (www.consort-statement.org). Future randomised clinical trials ought to include people at higher anaesthetic risk eligible for liver resection and to employ blinded assessments of outcomes. |

# Acknowledgements

We thank the Cochrane Comparing of Multiple Interventions Methods Group and the Cochrane Hepato-Biliary Group for their support and advice.

Peer reviewers of review: Emmanouil Giorgakis, UK; Aleksander Krag, Denmark.

Peer reviewers of protocol: Christopher Schmid, USA; Kristian Thorlund, Canada.

Contact editor: Christian Gluud, Denmark.

# Data and analyses

This review has no analyses.

# Appendices

## Appendix 1. Search strategies

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## Appendix 2. Winbugs code

### Binary outcome - fixed-effect model

# Binomial likelihood, logit link

# Fixed effects model

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

mu[i] ˜ dnorm(0,.0001) # vague priors for all trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

r[i,k] ˜ dbin(p[i,k],n[i,k]) # binomial likelihood

# model for linear predictor

logit(p[i,k]) <- mu[i] + d[t[i,k]] - d[t[i,1]]

# expected value of the numerators

rhat[i,k] <- p[i,k] * n[i,k]

#Deviance contribution

dev[i,k] <- 2 * (r[i,k] * (log(r[i,k])-log(rhat[i,k]))

+ (n[i,k]-r[i,k]) * (log(n[i,k]-r[i,k]) - log(n[i,k]-rhat[i,k])))

}

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

}

totresdev <- sum(resdev[]) # Total Residual Deviance

d[1]<-0 # treatment effect is zero for reference treatment

# vague priors for treatment effects

for (k in 2:nt){ d[k] ˜ dnorm(0,.0001) }

# ranking on relative scale

for (k in 1:nt) {

# rk[k] <- nt+1-rank(d[],k) # assumes events are “good”

rk[k] <- rank(d[],k) # assumes events are “bad”

best[k] <- equals(rk[k],1) #calculate probability that treat k is best

for (h in 1:nt){ prob[h,k] <- equals(rk[k],h) } # calculates probability that treat k is h-th best

}

} # *** PROGRAM ENDS

### Binary outcome - random-effects model

# Binomial likelihood, logit link

# Random effects model for multi-arm trials

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

w[i,1] <- 0 # adjustment for multi-arm trials is zero for control arm

delta[i,1] <- 0 # treatment effect is zero for control arm

mu[i] ˜ dnorm(0,.0001) # vague priors for all trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

r[i,k] ˜ dbin(p[i,k],n[i,k]) # binomial likelihood

logit(p[i,k]) <- mu[i] + delta[i,k] # model for linear predictor

rhat[i,k] <- p[i,k] * n[i,k] # expected value of the numerators

#Deviance contribution

dev[i,k] <- 2 * (r[i,k] * (log(r[i,k])-log(rhat[i,k]))

+ (n[i,k]-r[i,k]) * (log(n[i,k]-r[i,k]) - log(n[i,k]-rhat[i,k]))) }

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

for (k in 2:na[i]) { # LOOP THROUGH ARMS

# trial-specific LOR distributions

delta[i,k] ˜ dnorm(md[i,k],taud[i,k])

# mean of LOR distributions (with multi-arm trial correction)

md[i,k] <- d[t[i,k]] - d[t[i,1]] + sw[i,k]

# precision of LOR distributions (with multi-arm trial correction)

taud[i,k] <- tau *2*(k-1)/k

# adjustment for multi-arm RCTs

w[i,k] <- (delta[i,k] - d[t[i,k]] + d[t[i,1]])

# cumulative adjustment for multi-arm trials

sw[i,k] <- sum(w[i,1:k-1])/(k-1)

}

}

totresdev <- sum(resdev[]) # Total Residual Deviance

d[1]<-0 # treatment effect is zero for reference treatment

# vague priors for treatment effects

for (k in 2:nt){ d[k] ˜ dnorm(0,.0001) }

sd ˜ dunif(0,5) # vague prior for between-trial SD

tau <- pow(sd,-2) # between-trial precision = (1/between-trial variance)

# ranking on relative scale

for (k in 1:nt) {

# rk[k] <- nt+1-rank(d[],k) # assumes events are “good”

rk[k] <- rank(d[],k) # assumes events are “bad”

best[k] <- equals(rk[k],1) #calculate probability that treat k is best

for (h in 1:nt){ prob[h,k] <- equals(rk[k],h) } # calculates probability that treat k is h-th best

}

} # *** PROGRAM ENDS

### Binary outcome - inconsistency model (random-effects)

# Binomial likelihood, logit link, inconsistency model

# Random effects model

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

delta[i,1]<-0 # treatment effect is zero in control arm

mu[i] ˜ dnorm(0,.0001) # vague priors for trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

r[i,k] ˜ dbin(p[i,k],n[i,k]) # binomial likelihood

logit(p[i,k]) <- mu[i] + delta[i,k] # model for linear predictor

#Deviance contribution

rhat[i,k] <- p[i,k] * n[i,k] # expected value of the numerators

dev[i,k] <- 2 * (r[i,k] * (log(r[i,k])-log(rhat[i,k]))

+ (n[i,k]-r[i,k]) * (log(n[i,k]-r[i,k]) - log(n[i,k]-rhat[i,k])))

}

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

for (k in 2:na[i]) { # LOOP THROUGH ARMS

# trial-specific LOR distributions

delta[i,k] ˜ dnorm(d[t[i,1],t[i,k]] ,tau)

}

}

totresdev <- sum(resdev[]) # Total Residual Deviance

for (c in 1:(nt-1)) { # priors for all mean treatment effects

for (k in (c+1):nt) { d[c,k] ˜ dnorm(0,.0001) }

}

sd ˜ dunif(0,5) # vague prior for between-trial standard deviation

var <- pow(sd,2) # between-trial variance

tau <- 1/var # between-trial precision

} # *** PROGRAM ENDS

### Continuous outcome - fixed-effect model

# Normal likelihood, identity link

# Fixed effects model

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

mu[i] ˜ dnorm(0,.0001) # vague priors for all trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

var[i,k] <- pow(se[i,k],2) # calculate variances

prec[i,k] <- 1/var[i,k] # set precisions

y[i,k] ˜ dnorm(theta[i,k],prec[i,k]) # binomial likelihood

# model for linear predictor

theta[i,k] <- mu[i] + d[t[i,k]] - d[t[i,1]]

#Deviance contribution

dev[i,k] <- (y[i,k]-theta[i,k])*(y[i,k]-theta[i,k])*prec[i,k]

}

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

}

totresdev <- sum(resdev[]) #Total Residual Deviance

d[1]<-0 # treatment effect is zero for control arm

# vague priors for treatment effects

for (k in 2:nt){ d[k] ˜ dnorm(0,.0001) }

# ranking on relative scale

for (k in 1:nt) {

# rk[k] <- nt+1-rank(d[],k) # assumes events are “good”

rk[k] <- rank(d[],k) # assumes events are “bad”

best[k] <- equals(rk[k],1) #calculate probability that treat k is best

for (h in 1:nt){ prob[h,k] <- equals(rk[k],h) } # calculates probability that treat k is h-th best

}

} # *** PROGRAM ENDS

### Continuous outcome - random-effects model

# Normal likelihood, identity link

# Random effects model for multi-arm trials

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

w[i,1] <- 0 # adjustment for multi-arm trials is zero for control arm

delta[i,1] <- 0 # treatment effect is zero for control arm

mu[i] ˜ dnorm(0,.0001) # vague priors for all trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

var[i,k] <- pow(se[i,k],2) # calculate variances

prec[i,k] <- 1/var[i,k] # set precisions

y[i,k] ˜ dnorm(theta[i,k],prec[i,k]) # binomial likelihood

theta[i,k] <- mu[i] + delta[i,k] # model for linear predictor

#Deviance contribution

dev[i,k] <- (y[i,k]-theta[i,k])*(y[i,k]-theta[i,k])*prec[i,k]

}

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

for (k in 2:na[i]) { # LOOP THROUGH ARMS

# trial-specific LOR distributions

delta[i,k] ˜ dnorm(md[i,k],taud[i,k])

# mean of LOR distributions, with multi-arm trial correction

md[i,k] <- d[t[i,k]] - d[t[i,1]] + sw[i,k]

# precision of LOR distributions (with multi-arm trial correction)

taud[i,k] <- tau *2*(k-1)/k

# adjustment, multi-arm RCTs

w[i,k] <- (delta[i,k] - d[t[i,k]] + d[t[i,1]])

# cumulative adjustment for multi-arm trials

sw[i,k] <- sum(w[i,1:k-1])/(k-1)

}

}

totresdev <- sum(resdev[]) #Total Residual Deviance

d[1]<-0 # treatment effect is zero for control arm

# vague priors for treatment effects

for (k in 2:nt){ d[k] ˜ dnorm(0,.0001) }

sd ˜ dunif(0,5) # vague prior for between-trial SD

tau <- pow(sd,-2) # between-trial precision = (1/between-trial variance)

# ranking on relative scale

for (k in 1:nt) {

# rk[k] <- nt+1-rank(d[],k) # assumes events are “good”

rk[k] <- rank(d[],k) # assumes events are “bad”

best[k] <- equals(rk[k],1) #calculate probability that treat k is best

for (h in 1:nt){ prob[h,k] <- equals(rk[k],h) } # calculates probability that treat k is h-th best

}

} # *** PROGRAM ENDS

### Continuous outcome - inconsistency model (random-effects)

# Normal likelihood, identity link

# Random effects model for multi-arm trials

model{ # *** PROGRAM STARTS

for(i in 1:ns){ # LOOP THROUGH STUDIES

delta[i,1] <- 0 # treatment effect is zero for control arm

mu[i] ˜ dnorm(0,.0001) # vague priors for all trial baselines

for (k in 1:na[i]) { # LOOP THROUGH ARMS

var[i,k] <- pow(se[i,k],2) # calculate variances

prec[i,k] <- 1/var[i,k] # set precisions

y[i,k] ˜ dnorm(theta[i,k],prec[i,k]) # binomial likelihood

theta[i,k] <- mu[i] + delta[i,k] # model for linear predictor

#Deviance contribution

dev[i,k] <- (y[i,k]-theta[i,k])*(y[i,k]-theta[i,k])*prec[i,k]

}

# summed residual deviance contribution for this trial

resdev[i] <- sum(dev[i,1:na[i]])

for (k in 2:na[i]) { # LOOP THROUGH ARMS

# trial-specific LOR distributions

delta[i,k] ˜ dnorm(d[t[i,1],t[i,k]] ,tau)

}

}

totresdev <- sum(resdev[]) # Total Residual Deviance

for (c in 1:(nt-1)) { # priors for all mean treatment effects

for (k in (c+1):nt) { d[c,k] ˜ dnorm(0,.0001) }

}

sd ˜ dunif(0,5) # vague prior for between-trial standard deviation

tau <- pow(sd,-2) # between-trial precision

} # *** PROGRAM ENDS

## Appendix 3. Raw data

### Legend

#### Binary outcomes

# ns= number of studies; nt=number of treatments; t[,1] indicates control and t[,2] indicates intervention. In a three-arm trial, t[,3] indicates the second intervention. r[,1] indicates the number with events in the control group; n[,1] indicates the total number of people in the control group. r[,2], n[,2], r[,3], and n[,3] indicate the corresponding numbers for intervention and second intervention. In two-arm trials, r[,3] and n[,3] will be entered as 'NA' to indicate empty cells. If no three-arm trials were included under the outcome, the entire columns r[,3] and n[,3] were not included. na[] indicates the number of arms in the trial. Study indicates the study name and is for reference only.

#### # Continuous outcomes

# ns= number of studies; nt=number of treatments; t[,1] indicates control and t[,2] indicates intervention. In a three-arm trial, t[,3] indicates the second intervention. y[,1] indicates the mean in the control group; se[,1] indicates the standard error in the control group. y[,2], se[,2], y[,3], and se[,3] indicate the corresponding numbers for intervention and second intervention. In two-arm trials, y[,3] and se[,3] will be entered as 'NA' to indicate empty cells. If no three-arm trials were included under the outcome, the entire columns r[,3] and n[,3] were not included. na[] indicates the number of arms in the trial. Study indicates the study name and is for reference only.

### Mortality (binary outcome)

# Treatment codes: 1: NoVascClampNoFib; 2: NoVascCUSANoFib; 3: NoVascRFAblNoFib; 4: ContVascClampNoFib; 5: ContVascSharpNoFib; 6: IntVascClampNoFib; 7: IntVascCUSANoFib

# ns= number of studies; nt=number of treatments

list(ns=7, nt=7)

r[,1] n[,1] r[,2] n[,2] r[,3] n[,3] t[,1] t[,2] t[,3] na[] #study

1.5 37 0.5 38 NA NA 4 6 NA 2 #Petrowsky

2.5 26 0.5 26 0.5 26 2 3 4 3 #Lesurtel

0.5 27 0.5 25 NA NA 1 3 NA 2 #Lupo

0.5 42 0.5 42 NA NA 4 5 NA 2 #Smyrniotis

1 63 1 63 NA NA 1 6 NA 2 #Capussotti

2.5 21 0.5 21 NA NA 6 7 NA 2 #Doklestic

0.5 26 0.5 26 NA NA 2 7 NA 2 #Park

END

### Serious adverse events (binary outcome)

# Treatment codes: 1: NoVascClampNoFib; 2: NoVascCUSANoFib; 3: NoVascRFAblNoFib; 4: ContVascClampNoFib; 5: ContVascSharpNoFib; 6: IntVascClampNoFib

list(ns=5, nt=6)

r[,1] n[,1] r[,2] n[,2] r[,3] n[,3] t[,1] t[,2] t[,3] na[] #study

2 36 2 37 NA NA 4 6 NA 2 #Petrowsky

2 25 3 25 4 25 2 3 4 3 #Lesurtel

2 26 12 24 NA NA 1 3 NA 2 #Lupo

1 41 1 41 NA NA 4 5 NA 2 #Smyrniotis

4 63 2 63 NA NA 1 6 NA 2 #Capussotti

END

### Blood transfusion proportion (binary outcome)

list(ns=6, nt=7)

r[,1] n[,1] r[,2] n[,2] r[,3] n[,3] t[,1] t[,2] t[,3] na[] #study

9 36 11 37 NA NA 4 6 NA 2 #Petrowsky

8 25 5 25 1 25 2 3 4 3 #Lesurtel

13 26 8 24 NA NA 1 3 NA 2 #Lupo

15 41 13 41 NA NA 4 5 NA 2 #Smyrniotis

1 63 8 63 NA NA 1 6 NA 2 #Capussotti

2 20 3 20 NA NA 6 7 NA 2 #Doklestic

END

### Blood transfusion quantity (continuous outcome)

list(ns=2, nt=3)

t[,1] t[,2] y[,1] y[,2] se[,1] se[,2] na[] # study

1 3 1.7 2.9 0.3 0.49 2 # Petrowsky

2 1 0 0 0.49 0.49 2 # Smyrniotis SE imputed

END

### Operative blood loss (continuous outcome)

list(ns=3, nt=4)

t[,1] t[,2] y[,1] y[,2] se[,1] se[,2] na[] # study

2 4 426 492 75 75.6 2 # Petrowsky

2 3 460 500 75.6 75.6 2 # Smyrniotis

1 4 204.1 184.1 23.3 31.3 2 # Capussotti

END

### Hospital stay (continuous outcome)

list(ns=6, nt=7)

t[,1] t[,2] t[,3] y[,1] y[,2] y[,3] se[,1] se[,2] se[,3] na[] # study

4 6 NA 14.7 12.7 NA 1.6 1.4 NA 2 # Petrowsky

2 3 4 9 9 9 1.6 1.6 1.6 3 # Lesurtel SE imputed

4 5 NA 10 11 NA 1.6 1.6 NA 2 # Smyrniotis SE imputed

1 6 NA 8.6 8.9 NA 0.4 0.6 NA 2 # Capussotti

6 7 NA 10 8.5 NA 1.6 1.6 NA 2 # Doklestic SE imputed

2 7 NA 19.3 15.8 NA 1.4 0.9 NA 2 # Park

END

### Intensive therapy unit stay (continuous outcome)

list(ns=4, nt=6)

t[,1] t[,2] t[,3] y[,1] y[,2] y[,3] se[,1] se[,2] se[,3] na[] # study

3 5 NA 4 1.8 NA 1.2 0.5 NA 2 # Petrowsky

1 2 3 1 1 1 1.2 1.2 1.2 3 # Lesurtel SE imputed

3 4 NA 1 1 NA 1.2 1.2 NA 2 # Smyrniotis SE imputed

5 6 NA 1.5 0 NA 1.2 1.2 NA 2 # Doklestic SE imputed

END

### Operating time (continuous outcome)

list(ns=4, nt=5)

t[,1] t[,2] y[,1] y[,2] se[,1] se[,2] na[] # study

2 4 316 300 21 19.1 2 # Petrowsky

2 3 211 205 21 21 2 # Smyrniotis SE imputed

4 5 240 270 21 21 2 # Doklestic SE imputed

1 5 338.9 387.2 7.9 6.6 2 # Park

END

## Appendix 4. Technical details of network meta-analysis

The posterior probabilities (effect estimates or values) of the treatment contrast (i.e., log odds ratio or mean difference) may vary depending upon the initial values to start the simulations. In order to control the random error due to the choice of initial values, we performed the network analysis for three different initial values (priors) as per the guidance from The National Institute for Health and Care Excellence (NICE) Decision Support Unit (DSU) documents (Dias 2013). If the results from three different priors are similar (convergence), then the results are reliable. It is important to discard the results of the initial simulations as they can be significantly affected by the choice of the priors and only include the results of the simulations obtained after the convergence. The discarding of the initial simulations is called 'burn in'. We ran the models for all binary outcomes for 30,000 simulations for 'burn in' for three different chains (a set of initial values). We ran the models for another 100,000 simulations to obtain the effect estimates. For continuous outcomes, we ran the model for 100,000 simulations for 'burn in' for three different chains and for another 300,000 simulations to obtain the effect estimates. The exceptions for this were operating time and operative blood loss where the random-effects models did not converge until 400,000. We ran a further 300,000 simulations to obtain the effect estimates. We obtained the effect estimates from the results of all the three chains (different initial values). We also ensured that the results in the three different chains were similar in order to control for random error due to the choice of priors. This was done in addition to the visual inspection of convergence obtained after simulations in the burn in.

We ran three different models for each outcome. Fixed-effect model assumes that the treatment effect is the same across studies. The random-effects consistency model assumes that the treatment effect is distributed normally across the studies but assumes that the transitivity assumption is satisfied (i.e., the population studied, the definition of outcomes, and the methods used were similar across studies and that there is consistency between the direct comparison and indirect comparison). A random-effects inconsistency model does not assume transitivity assumption. If the inconsistency model resulted in a better model fit than the consistency model, the results of the network meta-analysis can be unreliable and so should be interpreted with extreme caution. If there was evidence of inconsistency, we planned to identify areas in the network where substantial inconsistency might be present in terms of clinical and methodological diversities between trials and, when appropriate, limit network meta-analysis to a more compatible subset of trials.

The choice of the model between fixed-effect model and random-effects model was based on the model fit as per the guidelines of the NICE TSU (Dias 2013). The model fit was assessed by deviance residuals and Deviance Information Criteria (DIC) according to NICE TSU guidelines (Dias 2013). A difference of three or five in the DIC is not generally considered important (Dias 2012b). We used the simpler model, that is, fixed-effect model was used if the DIC were similar between the fixed-effect model and random-effects model. We used the random-effects model if it resulted in a better model fit as indicated by a DIC lower than that of fixed-effect model by at least three.

We have calculated the effect estimates of the treatment and the 95% credible intervals using the formulae for calculating the effect estimates in indirect comparisons (Bucher 1997):

ln(OR_{AC}) = ln(OR_{AB}) - ln(OR_{CB}) and

Var(ln OR_{AC}) = Var (ln OR_{AB}) + Var (ln OR_{CB})

where ln indicates natural logarithm; OR indicates odds ratio; Var indicates variance; and A, B, and C are three different treatments.

## Appendix 5. Sample size calculation

The required information size for the outcome measure of perioperative mortality was 20,116 participants based on a perioperative mortality proportion of 3.5% in the control group (Finch 2007), a relative risk reduction of 20% in the experimental group, type I error of 5%, and type II error of 20%. Network analyses may be more prone to the risk of random errors than direct comparisons (Del Re 2013). Accordingly, a greater sample size is required in indirect comparisons than direct comparisons (Thorlund 2012). The power and precision in indirect comparisons depends upon various factors such as the number of participants included under each comparison and the heterogeneity between the trials (Thorlund 2012). If there was no heterogeneity across the trials, the sample size in indirect comparisons would be equivalent to the sample size in direct comparisons. The effective indirect sample size can be calculated using the number of participants included in each direct comparison (Thorlund 2012). For example, a sample size of 2500 participants in the direct comparison A versus C (n_{AC}) and a sample size of 7500 participants in the direct comparison B versus C (n_{BC}) results in an effective indirect sample size of 1876 participants. However, in the presence of heterogeneity within the comparisons, the sample size required is higher. In the above scenario, for an I^{2} statistic for each of the comparisons A versus C (I_{AC}^{2}) and B versus C (I_{BC}^{2}) of 25%, the effective indirect sample size is 1407 participants. For an I^{2} statistic for each of the comparisons A versus C and B versus C of 50%, the effective indirect sample size is 938 participants (Thorlund 2012). We planned to calculate the effective indirect sample size using the following generic formula (Thorlund 2012):

((n_{AC} x (1 - I_{AC}^{2})) x (n_{BC} x (1-I_{BC}^{2}))/((n_{AC} x (1 - I_{AC}^{2})) + (n_{BC} x (1-I_{BC}^{2})).

However, we did not perform this as the number of participants included in this network analysis is less than that needed in a direct comparison. In addition, there is currently no method to calculate the effective indirect sample size for a network analysis involving more than three treatment groups.

# Contributions of authors

Constantinos Simillis identified the studies, extracted the data, performed part of the analysis, and drafted the review.

Tianjing Li critically reviewed the content, particularly in relation to the network meta-analysis.

Lorne A Becker and Brian R Davidson critically commented on the review.

Kurinchi S Gurusamy performed the analysis and revised the review.

All review authors agreed on this version before publication.

Kurinchi S Gurusamy drafted the protocol, which was carefully reviewed and revised by Tianjing Li. Tianjing Li also wrote the sections related to network meta-analysis. The protocol was developed after discussion with Lorne A Becker and Brian R Davidson. All review authors agreed on this version before publication.

# Declarations of interest

Review authors perform research related to decreasing blood loss in liver resection. This includes clinical studies.

# Sources of support

## Internal sources

- University College London, UK.

## External sources

- National Institute for Health Research, UK.National Institute for Health Research, the health research wing of the UK Government Department of Health funds K Gurusamy to complete this review.

# Differences between protocol and review

- We calculated the odds ratios (OR) rather than the risk ratios (RR) since it is easier to model the OR for network meta-analysis. Although ORs are more difficult to interpret than RRs, we have overcome this problem with interpretation by presenting the results as illustrative comparative risks for mortality, serious adverse events, and proportion of people with blood transfusion.
- We have calculated the mean difference (MD) and 95% credible interval (CrI) for quantity of blood transfused rather than the standardised mean difference (SMD) and 95% CrI. We expected some authors report quantity of blood transfused in litres transfused and others to report this as number of units transfused. However, all the trials included in this review reported the quantity of blood transfused in units enabling us to calculate the MD and 95% CrI, which is easier to interpret than SMD.
- We planned to calculated to calculate the rate ratio (RaR) with 95% CrI. However, the trials reported the proportion of people with serious adverse events. So we calculated the OR with 95% CrI rather than RaR with 95% CrI.
- We used the residual deviance and Deviance Information Criteria (DIC) for assessing between-study heterogeneity as per the guidance from the National Institute for Health and Care Excellence (NICE) Decision Support Unit (DSU) Technical Support Documents (Dias 2012b; Dias 2013).
- We have reported the network meta-analysis on all the outcomes although we planned to perform the network analysis for the primary outcomes and one secondary outcome on blood transfusion requirements. This was to obtain and report the maximum information from the available data.
- We planned to report the random-effects model for network meta-analysis. However, we decided to report the fixed-effect model or random-effects model based on residual deviance and DIC statistics as recommended by the NICE DSU Technical Support Documents (Dias 2013).
- We did not fit the inconsistency model that uses the design-by-treatment approach proposed by Whites and Higgins (Higgins 2012; White 2012), since we performed all the analyses using the Bayesian framework.
- We did not first calculate all pair-wise meta-analysis estimates and then compare them with indirect comparison estimates (Bucher 1997) for each loop as the method that we used is an extension of the Bucher et al. (Bucher 1997) method to assess inconsistency (Dias 2012c).
- We did not perform the direct comparison. This was because of the exclusion of many trials that might have been suitable for direct comparison but were unsuitable for the overview.

# Notes

Considerable overlap is evident in the background and methods sections of this review and those of several other reviews written by the same group of authors.

Author order was changed in August 2013: Constantinos Simillis, Tianjing Li, Jessica Vaughan, Lorne Becker, Brian Davidson, Kurinchi Gurusamy.

# Index terms

## Medical Subject Headings (MeSH)

Bayes Theorem; Blood Loss, Surgical [*prevention & control]; Blood Transfusion [utilization]; Catheter Ablation [methods]; Fibrin Tissue Adhesive [administration & dosage]; Hemostasis, Surgical [*methods]; Hepatectomy [adverse effects; *methods]; Randomized Controlled Trials as Topic; Suction [instrumentation; methods]

## MeSH check words

Humans

* Indicates the major publication for the study