Description of the condition
Hepatorenal syndrome is kidney failure developing in patients with advanced cirrhosis or fulminant hepatic impairment as a consequence of severe renal vasoconstriction (Kjaergard 2003; Guevara 2011; Wadei 2012). Haemodynamic changes present early in patients with liver disease. Besides renal vasoconstriction, circulatory failure resulting in cardiac dysfunction has recently been recognised as playing an important role in the hepatorenal syndrome. This condition is characterised by cirrhosis with ascites; serum creatinine more than 133 mmol/L (1.5 mg/dL); no decrease of serum creatinine to a level of less than or equal to 133 mmol/L after at least two days from diuretic withdrawal and volume expansion with albumin; absence of shock; no current or recent treatment with nephrotoxic drugs; and absence of kidney disease (proteinuria more than 500 mg/day, microhaematuria, and/or abnormal renal ultrasonography) (Arroyo 2008).
There are two types of hepatorenal syndromes. Both type 1 and type 2 hepatorenal syndromes present with intrarenal vasoconstriction due to the haemodynamic alterations caused by severe liver failure and portal hypertension. Type 1 hepatorenal syndrome is a rapidly progressive renal failure, occurring in days, frequently associated with failure in other organs (mainly heart, brain, or liver). By contrast, type 2 hepatorenal syndrome is a steady and moderate renal failure where the main clinical problem is refractory ascites (Guevara 2011). The annual incidence of hepatorenal syndrome in patients with cirrhosis and ascites is estimated to be 8% (Arroyo 2008). Renal histology shows no lesions that explain the impairment in the renal function. It occurs in the setting of a severe circulatory dysfunction with arterial hypotension and intense stimulation of hormone secretion (renin-angiotensin, sympathetic nervous system, and antidiuretic hormone) (Arroyo 2008). There are two key features in the pathogenesis of hepatorenal syndrome; the first mechanism is the intense dilatation or the arteries in the splanchnic territory, resulting in the pooling of blood in this area, and the second is the reduction of blood ejected by the heart, caused by an alteration in its muscle fibres due to cirrhosis (Hasper 2011). A false diagnosis of hepatorenal syndrome is common. One has to meticulously exclude other disorders that can cause renal failure in cirrhosis to reach the correct diagnosis.
Untreated, median survival is two weeks for patients with type 1 hepatorenal syndrome and four to six months in patients with type 2 hepatorenal syndrome (Gines 2003). Therapeutic efforts are designed to increase renal perfusion and mean arterial blood pressure, and include vasopressors as terlipressin and albumin (Davenport 2012; Gluud 2012). Because of its overall poor prognosis, hepatorenal syndrome is better prevented than treated. Preventive strategies include the administration of albumin following large-volume paracentesis (more or equal to 5 L of ascites) and pentoxifylline in patients with alcoholic hepatitis (Whitfield 2009; Wadei 2012). Other therapeutic options include midodrine, norepinephrine, liver transplant, and transjugular intrahepatic portosystemic shunts.
Description of the intervention
Liver transplantation is the treatment of choice for any patient with advanced cirrhosis, including those with type 1 and type 2 hepatorenal syndrome. The ideal goals of treatment for hepatorenal syndrome are to prolong survival until a liver donor becomes available, and to optimise conditions for successful liver transplantation with vasoconstrictors and occasionally transjugular intrahepatic portosystemic shunts (Arroyo 2008; Wadei 2012).
Conventional management of hepatorenal syndrome patients
Type 1 hepatorenal syndrome patients need to be managed in an intensive care unit because these patients have multiorgan failure and deteriorate rapidly. Type 2 hepatorenal syndrome patients usually can be treated in a non-intensive care setting or as an outpatient. Management goal is to maintain intravascular volume with exogenous albumin. Synthetic plasma expanders are not recommended.
Intravenous terlipressin and albumin infusion constitute the treatment of choice for hepatorenal syndrome patients in Europe (Appendix 1). Whether the evidence is strong enough to support the use of terlipressin for clinical practice could be debated due to the results of a trial sequential analysis performed in a Cochrane systematic review (Gluud 2012). Alessandria 2002 concluded that terlipressin might be useful when selecting cirrhotic patients with renal failure as candidates for a transjugular intrahepatic portosystemic shunt or liver transplantation. Other vasoconstrictors used in hepatorenal syndrome are octreotide with midodrine (Appendix 1). A study that analysed the efficacy of midodrine concluded that patients treated with octreotide, midodrine, and albumin presented improvement in kidney function and greater likelihood for liver transplantation compared with the no treatment group (Skagen 2009). Another vasoconstrictor used for hepatorenal syndrome patients is intravenous norepinephrine in combination with albumin and furosemide with good results in renal function and mortality (Duvoux 2002). However, despite their broad use, a meta-analysis from 2010 has shown no differences between several vasoconstrictors and patient survival (Gluud 2010).
Transjugular intrahepatic portosystemic shunts
Transjugular intrahepatic portosystemic shunts is a portal decompression method that involves inserting intrahepatic prosthesis between portal and hepatic veins through transjugular approach. The main adverse effects comprise encephalopathy and complications related to the procedure (bleeding, vascular perforation). Studies have reported improvement for type 1 and 2 hepatorenal syndrome patients (Salerno 2007; Rössle 2010; Wadei 2012).
How the intervention might work
A transjugular intrahepatic portosystemic shunt decreases portal pressure and favours the return of blood volume from the splanchnic territory to systemic circulation, decreasing the amount of blood in the splanchnic vascular bed, thus suppressing the activity of renin-angiotensin aldosterone system and sympathetic nervous system. This reduces the vasoconstrictor effect these systems have on the renal circulation. The effect of transjugular intrahepatic portosystemic shunts improving urinary sodium excretion and renal function in cirrhotic patients with refractory ascites is well documented (Wong 1995; Jalan 1996; Gerbes 1998). Other benefits, such as improvement in renal perfusion, reduced portal pressure, and plasma norepinephrine levels, have been demonstrated (Stadlbauer 2008).
Efficacy of transjugular intrahepatic portosystemic shunts in hepatorenal syndrome
Studies evaluating the effect of a transjugular intrahepatic portosystemic shunt in type 1 hepatorenal syndrome and preserved liver function have shown marked reduction of portal pressure gradient and improvement of renal function 30 days after the transjugular intrahepatic portosystemic shunt compared to conventional therapy (Guevara 1998). Other studies have demonstrated similar benefits, and, following the transjugular intrahepatic portosystemic shunt, 3, 6, 12, and 18 months survival was higher with the transjugular intrahepatic portosystemic shunt compared to conventional therapy (Brensing 2000). An important observation from these two studies is the slow and delayed recovery of renal function following the transjugular intrahepatic portosystemic shunt (within two to four weeks), unlike vasoconstrictor therapy, in which responders have faster recovery of renal function (one to two weeks). The results of these studies suggest that transjugular intrahepatic portosystemic shunts improve renal function in patients with type 1 hepatorenal syndrome and in the majority of non-transplantable cirrhotics with hepatorenal syndrome. Adverse events reported with a transjugular intrahepatic portosystemic shunt insertion in patients with type 2 hepatorenal syndrome include fever and vomiting (Testino 2003). Hepatic encephalopathy is the main complication and the one that, if present prior to transjugular intrahepatic portosystemic shunt insertion, will worsen after the intervention. Another study evaluated combined therapy with vasoconstrictors and transjugular intrahepatic portosystemic shunts in type 1 hepatorenal syndrome and demonstrated that patients with transjugular intrahepatic portosystemic shunts improved renal function and sodium excretion in 12 months (Wong 2004). These results suggest that transjugular intrahepatic portosystemic shunts are not necessarily an alternative for patients not candidates to vasoconstrictors, but that these patients often benefit from the intervention.
Why it is important to do this review
Most studies have been conducted to evaluate the efficacy and safety of vasopressors and albumin for the management of hepatorenal syndrome. However, information regarding the beneficial and harmful effects of transjugular intrahepatic portosystemic shunts is inconclusive. The purpose of this review is, therefore, to evaluate the efficacy and safety of transjugular intrahepatic portosystemic shunts for patients with hepatorenal syndrome to reduce morbidity and mortality.
To assess the benefits and harms of transjugular intrahepatic portosystemic shunts in patients with liver cirrhosis and hepatorenal syndrome versus sham or no intervention or versus conventional therapies (combination of octreotide, midodrine, terlipressin, norepinephrine, albumin, and paracentesis) to other therapies (pharmacologic therapy).
Criteria for considering studies for this review
Types of studies
Randomised clinical trials that assess a transjugular intrahepatic portosystemic shunt insertion in patients with hepatorenal syndrome. If quasi-randomised studies or other observational studies are identified with the searches for randomised clinical trials, then we will include these publications only for data on harm.
Types of participants
Adult participants at the age of 18 or above, all sexes, all ethnic groups, with chronic hepatic cirrhosis (any cause) and hepatorenal syndrome type 1 or 2 requiring transjugular intrahepatic portosystemic shunts (all indications), ambulatory or in ward.
We will exclude participants with renal failure by other cause, not related to the hepatorenal syndrome.
Types of interventions
- Transjugular intrahepatic portosystemic shunt versus sham or no intervention
- Transjugular intrahepatic portosystemic shunt versus conventional therapy (combinations of octreotide, midodrine, terlipressin, norepinephrine, albumin, and paracentesis)
Types of outcome measures
We will assess the following outcomes at 30 days, three months, one year, or at the maximum follow-up of the trials.
- Adverse events: serious adverse events will be defined according to the International Conference on Harmonisation of Technical Requirements for Registration of Pharmaceuticals for Human Use (ICH) as any untoward medical occurrence that at any dose resulted in death, was life-threatening, required inpatient hospitalisation or prolongation of existing hospitalisation, or resulted in persistent or significant disability or incapacity, or was a congenital anomaly/birth defect, or any medical event, which might have jeopardised the patient, or required intervention to prevent it (ICH-GCP 1996). All other adverse events (that is, any medical occurrence not necessarily having a causal relationship with the treatment but did, however, cause a dose reduction or discontinuation of the treatment) will be considered non-serious.
- Quality of life.
- Number of participants with non-serious adverse events associated with the transjugular intrahepatic portosystemic shunts (acute and chronic).
- Number of patients undergoing liver transplantation.
- Participants without improved renal function (glomerular filtration rate in mL/min, serum creatinine in mg/dL, and blood urea nitrogen in mg/dL), and without improvement of encephalopathy (West-Haven classification).
- Length of hospitalisation (days).
Search methods for identification of studies
We will search the Cochrane Hepato-Biliary Group Controlled Trials Register (Gluud 2014), the Cochrane Central Register of Controlled Trials (CENTRAL)(latest issue), MEDLINE (1946 to date), EMBASE (1974 to date), Science Citation Index Expanded (1900 to date) (Royle 2003), LILACS (1980 to date), and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) search portal (apps.who.int/trialsearch/). Preliminary search strategies with the expected time spans of the searches are given in Appendix 2. The Cochrane Hepato-Biliary Group will assist with electronic searches where necessary. No language limitations will be applied.
Searching other resources
We will inspect the references of all identified studies for more trials. Additionally, we will contact the first or the corresponding author of each trial as well as researchers active in the field for information regarding unpublished trials and complementary data on their own trial (Egger 2003). No language limitations will be applied. Abstracts from the European Association for the Study of the Liver and American Association for the Study of the Liver Diseases conference meetings will be provided by the Cochrane Hepato-Biliary Group (Gluud 2014).
Data collection and analysis
Selection of studies
Two review authors will independently assess each reference identified by the search against the inclusion criteria. We plan to solve any disagreements that may arise through discussion. Those references that appear to meet the inclusion criteria will be retrieved in full for further independent assessment by the same review authors. If required, we will consult a third review author.
Data extraction and management
Two review authors will independently extract data from the included trials using a standardised data extraction form. Overall, we plan to extract the following data: eligibility criteria, demographics (age, sex, and country), characteristic of comorbidities and treatment. We will discuss any discrepancies between review authors and will achieve a final consensus. We will enter data into the Cochrane Collaboration's statistical software Review Manager 5 (RevMan 2012), and check them for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
The methodological quality is defined as the confidence that the trial design and its report restrict bias in the intervention comparison (Schulz 1995; Moher 1998; Kjaergard 2001). Due to the risk of overestimation of intervention effects in randomised trials with inadequate methodological quality (Schulz 1995; Moher 1998; Kjaergard 2001; Wood 2008; Lundh 2012; Savović 2012a; Savović 2012b), we will assess the influence of the below domains as reported in the trials (Jüni 2001). When this information is not available, we will ask the authors of the trial publications to provide it.
- 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 are adequate if performed by an independent research assistant not otherwise involved in the trial
- Uncertain risk of bias: The method of sequence generation was not specified
- High risk of bias: The sequence generation method was not random
- Allocation concealment
- Low risk of bias: The participant allocations could not have been foreseen in advance of, or during enrolment. Allocation was controlled by a central and independent randomisation unit. The allocation sequence was unknown to the investigators (for example, if the allocation sequence was hidden in sequentially numbered, opaque, and sealed envelopes)
- Uncertain risk of bias: 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: The allocation sequence was likely to be known to the investigators who assigned the participants
- Blinding of participants, personnel, and outcome assessors
- Low risk of bias: Blinding was performed adequately, or the assessment of outcomes was not likely to be influenced by lack of blinding
- Uncertain risk of bias: There was insufficient information to assess whether blinding was likely to induce bias on the results
- High risk of bias: No blinding or incomplete blinding, and the assessment of outcomes were likely to be influenced by lack of blinding
- Incomplete outcome data
- Low risk of bias: Missing data were unlikely to make treatment effects depart from plausible values. Sufficient methods, such as multiple imputation, has been employed to handle missing data
- Uncertain risk of bias: There was insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias on the results
- High risk of bias: The results were likely to be biased due to missing data
- Selective outcome reporting
- Low risk of bias: All outcomes were pre-defined and reported, or all clinically relevant and reasonably expected outcomes were reported
- Uncertain risk of bias: It is unclear whether all pre-defined and clinically relevant and reasonably expected outcomes were reported
- High risk of bias: One or more clinically relevant and reasonably expected outcomes were not reported, and data on these outcomes were likely to have been recorded
- For a trial to be assessed as having low risk of bias in the selective outcome reporting domain, the trial should have been registered either on ClinicalTrials.gov (clinicaltrials.gov/) or a similar register, or there should be a protocol, e.g., published in a paper journal. In the case of trials run and published in the years when trial registration was not required, we will carefully scrutinise all publications reporting on the trial to identify the trial objectives and outcomes. If usable data on all outcomes specified in the trial objectives are provided in the publication's results section, then the trial will be considered to have low risk of bias for the selective outcome reporting domain
- For-profit bias
- Low risk of bias: The trial appears to be free of industry sponsorship or other kind of for-profit support that may manipulate the trial design, conductance, or results of the trial
- Uncertain risk of bias: The trial may or may not be free of for-profit bias as no information on clinical trial support or sponsorship is provided
- High risk of bias: The trial is sponsored by the industry or has received other kind of for-profit support
- Other bias
- Low risk of bias: The trial appears to be free of other components (for example, academic bias) that could put it at risk of bias
- Uncertain risk of bias: The trial may or may not be free of other components that could put it at risk of bias
- High risk of bias: There are other factors in the trial that could put it at risk of bias (for example, authors have conducted trials on the same topic, etc)
We will judge the trials with low risk of bias if they fall within the definitions for low risk of bias in all domains. In all other cases, we will judge the trials with high risk of bias.
Measures of treatment effect
We will carry out statistical analysis using Review Manager 5 (RevMan 2012). Where possible, we will examine apparently significant beneficial and harmful intervention effects with trial sequential analyses (CTU 2011; Thorlund 2011) in order to evaluate if these apparent effects could be caused by random error (‘play of chance’) (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009, Wetterslev 2009; Thorlund 2010).
For dichotomous data, we will calculate the relative risks (RRs) with 95% confidence intervals (CIs). We will use a random-effects model and a fixed-effect model (DerSimonian 1986; DeMets 1987). In case of discrepancy between the two models (one giving a significant intervention effect, the other no significant intervention effect) we will report both results; otherwise, we will report only the results from one of the meta-analyses models.
For continuous data, we will use the mean differences (MDs) if outcomes are measured in the same way between trials. We will use the standardised mean differences (SMDs) to combine trials that measure the same outcome but use different methods. If there is evidence of skewed data, we will report it.
Unit of analysis issues
We will include cluster randomised trials in the analyses alongside with individually randomised trials. We will adjust their sample sizes using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), using an estimate of the intra cluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial, or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster randomised trials and individually randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the trials' designs and if the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely (Gluud 2008; Thorlund 2009).
We will also acknowledge heterogeneity in the randomisation unit and perform a subgroup analysis to investigate the effects of the randomisation unit.
Dealing with missing data
For included trials, we will note levels of attrition. We will explore the impact of including trials with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.
For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e., we will attempt to include all participants randomised to each group in the analyses, and all participants will be analysed in the group to which they were randomised, regardless of whether or not they received the allocated intervention (Hollis 1999). The denominator for each outcome in each trial will be the number of randomised participants minus any participants whose outcomes are known to be missing.
Where data are not reported for some outcomes or groups, we will attempt to contact the trial authors for further information.
Worst-best and best-worse intention-to-treat analyses
We will analyse data as reported in the trial, that is, either per protocol or as intention-to-treat analysis. In order to examine the influence of drop-outs, we will perform both worst-best case (assigning bad outcomes to all of the missing experimental group patients and good outcomes to all of the missing control group patients) and best-worst-case (assigning good outcomes to all of the missing experimental group patients and bad outcomes to all of the missing control group patients) analyses.
Assessment of heterogeneity
We will test for heterogeneity between trials, using the T
Assessment of reporting biases
Where we will suspect reporting bias (Assessment of risk of bias in included studies), we will attempt to contact trial authors asking them to provide missing outcome data. Where this is not possible and the missing data are thought to introduce serious bias, the impact of including such trials in the overall assessment of results will be explored by a sensitivity analysis.
Where we suspect publication bias (e.g., where only statistically significant results are reported), we will explore this using funnel plots (Macaskill 2001; Higgins 2011). We will involve the project statistician in the interpretation of such analysis. We will assess funnel plot asymmetry visually, and we will use formal tests for funnel plot asymmetry. For continuous outcomes, we will use the test proposed by Egger 1997, and for dichotomous outcomes, we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or is suggested by a visual assessment, we will perform exploratory analyses to investigate it.
We will carry out statistical analysis using Review Manager 5 (RevMan 2012).
We will use the fixed-effect and random-effects model meta-analyses, and in the case of statistically significant discrepancies in the results obtained through the two meta-analyses models, we will present both (Higgins 2011). The random-effects summary will be treated as the average range of possible treatment effects, and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.
If we use random-effects analyses, we will present the results as the average treatment effect with 95 % CIs and the I
Trial sequential analysis
Cumulative meta-analyses run the risks of random errors due to sparse data and repetitive testing when new trials emerge. Where possible, we will therefore examine the intervention effects with trial sequential analysis (CTU 2011; Thorlund 2011). This allows us to evaluate if these apparent effects could be caused by random error ('play of chance') (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010). To minimise random errors, we will calculate the diversity-adjusted required information size (i.e., the number of participants needed in a meta-analysis to detect or reject a certain intervention effect). The diversity-adjusted required information size calculation will also account for the diversity present in the meta-analysis. In our meta-analysis, the diversity-adjusted required information size will be based on the proportion of the events present in the control group; the assumption of a plausible RR reduction of 20% or the RR reduction observed in the included trials with low risk of bias; a risk of type I error of 5%, a risk of type II error of 20%, and the assumed diversity of the meta-analysis. The underlying assumption of trial sequential analysis is that testing for significance may be performed each time a new trial is added to the meta-analysis. We will add the trials according to the year of publication, and if more than one trial has been published in a year, trials will be added alphabetically according to the last name of the first author. On the basis of the required information size, trial sequential monitoring boundaries will be constructed. These boundaries will determine the statistical inference one may calculate regarding the cumulative meta-analysis that has not reached the required information size; if the trial sequential monitoring boundary is crossed before the required information size is reached, confident evidence may perhaps be established and further trials may turn out to be superfluous. On the other hand, if the boundary is not surpassed, it will probably be necessary to continue doing trials in order to detect or reject a certain intervention effect, if the area of futility has not been reached. This can be determined by assessing if the cumulative Z-curve crosses the trial sequential boundaries.
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use fixed-effect and random-effects analysis to produce effect estimates. We will restrict subgroup analyses to the primary outcomes.
We plan to carry out the following subgroup analyses:
- trials with low risk of bias compared to trials with high risk of bias;
- trials with blinded outcome assessment compared to trials without blinded outcome assessment;
- hepatorenal syndrome type 1 compared to hepatorenal syndrome type 2.
Sensitivity analyses are undertaken to explore the robustness of findings to key decisions in the review process. These will be determined as the review process takes place (Higgins 2011). We will perform sensitivity analyses to explore the influence of a trial's risk of bias on the results. We plan to conduct sensitivity analyses according to attrition bias, as estimated by the percentage of participants lost to follow-up.
Summary of findings tables
We will summarise the evidence for all binary outcomes in the 'Summary of Findings' tables according to the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach (Guyatt 2008).
Peer Reviewers: Hani Wadei, USA; Jorge Cerda, USA; Erwin Biecker, Germany.
Contact Editors: Luit Penninga, Denmark; Christian Gluud, Denmark.
Appendix 1. Glossary
- Terlipressin: (tri glycyl lysine vasopressin) is a synthetic analogue of vasopressin, which has been used in the treatment of acute variceal haemorrhage. In contrast to vasopressin, terlipressin can be administered as intermittent injections instead of continuous intravenous infusion and it has a safer adverse reactions profile. However, its effectiveness remains uncertain (Ioannou 2003).
- Midodrine: It is an agonist of the alpha-1 receptors used in the treatment of hypotension caused by dysfunction in the autonomic nervous system and severe orthostatism by increasing vascular tone and blood pressure.
Appendix 2. Search strategies
Contributions of authors
Alejandro González participated in the development of this protocol including the different methodological sections (form of search, types of analyses) that have been required to complete the necessary information and for the translation of the document from Spanish.
Norberto Chavez participated in the development of this protocol including the different sections and evaluation of literature with the aim of obtaining information of adequate methodological quality for the drafting of the background and the preparation of the synthesis of the literature.
Cecilia Solis searched for and retrieved the necessary articles at regional and global data bases that we used to carry out this protocol.
Andrea Hinojosa and Omar Salas, authors of this systematic review protocol, worked on the development of the protocol and its revisions until published.
Declarations of interest
Sources of support
- Library of National Institute of Pediatrics, Mexico.The library will keep providing us with articles that we need for the completion of this review.
- No sources of support supplied