Description of the condition
Severe bleeding can cause haemorrhagic shock, which is a lethal state of tissue hypoxia ultimately leading to cellular ischaemia and hence organ dysfunction, failure and death (Bruce 2008). An increasing number of patients annually receive oral anticoagulation therapy with a vitamin K antagonist such as warfarin or phenprocoumon in order to treat or prevent the incidence of venous thromboembolism. The primary medical indications are atrial fibrillation, venous thromboembolism and mechanical heart valves (Leissinger 2008; Levy 2008; Vang 2011). It is a widely used medical treatment requiring special consideration with regard to comorbidity, interacting medications and potentially lethal haemorrhagic complications. Large-scale epidemiological studies have shown an annual incidence of major bleeding complications from vitamin K antagonist treatment ranging from 1.1% to 1.5% with gastrointestinal, urinary and intracranial sites most frequently involved (Bruce 2008; Franchini 2010; Leissinger 2008; Palareti 1996). This is a potentially lethal condition requiring rapid reversal of oral anticoagulant therapy which has traditionally been executed by large transfusions of fresh frozen plasma. This strategy, however, poses important safety concerns such as volume overload, dilutional coagulopathy, blood group specificity, lack of viral inactivation and the risk of transfusion-related acute lung injury (Kor 2010; Leissinger 2008; Ozgonenel 2007).
Description of the intervention
Prothrombin complex concentrate was originally developed for the treatment of haemophilia B (Ostermann 2007). The increasing availability of purified and recombinant factor IX has transferred the use of prothrombin complex concentrate to other indications (Franchini 2010). Inhibition of the biosynthesis of vitamin K-dependent coagulation factors can be reversed using several treatment options. Withholding oral anticoagulation therapy and administering vitamin K induces hepatic de novo synthesis of vitamin K-dependent coagulation factors. In this context the normalization of haemostasis lasts hours to days. Fresh frozen plasma has generally been considered 'standard of care' for reversal of vitamin K antagonist therapy (Leissinger 2008). It provides partial reversal of the coagulopathy through replacement of exogenous factors II, VII, IX, and X but also poses important safety concerns and is challenging with regard to 'dosage/international normalized ratio (INR) correction' and time needed to prepare the infusion (Demeyere 2010; Holland 2006).
Prothrombin complex concentrate is derived from the cryoprecipitate supernatant of large plasma pools after removal of anti-thrombin and factor XI, and therefore represents a concentrate of all vitamin K-dependent clotting factors. Present-day prothrombin complex concentrates provide a source of vitamin K-dependent coagulation factors II, VII, IX and X and the naturally occurring anti-coagulants activated protein C and S. It has a final overall clotting factor concentration approximately 25 times higher than in normal plasma (Franchini 2010).
Prothrombin complex concentrate has come increasingly into focus with regard to the acute reversal of vitamin K antagonist bleeding disorders, and constitutes two complex clinical subgroups with a similar need for acute intervention but with different therapeutic indications (Levi 2009; Pindur 1999; Schick 2009; Vigué 2009):
- Vitamin K antagonist-treated patients with a bleeding complication requiring acute surgical intervention (e.g. intracranial bleeding);
- Vitamin K antagonist-treated patients with supranormal INR levels and no ongoing bleeding complication who have the need for acute surgical intervention .
How the intervention might work
The acute perioperative administration of prothrombin complex concentrate has been introduced within the past few years and is believed to minimize the need for blood transfusions, thereby reducing the risk of volume overload, haemodilution coagulopathy, transfusion-related acute lung injury and the possible transmission of viral infections (Bruce 2008; Franchini 2010; Riess 2007; Schick 2009).
Prothrombin complex concentrate theoretically offers several advantages compared to fresh frozen plasma: reduction in time required for the initiation of goal-directed therapeutic intervention (e.g. surgical intervention) since thawing of plasma is bypassed (Taberner 1976; Van Aart 2006); reduced infusion volume since prothrombin complex concentrate treatment of 1 to 2 ml/kg corresponds to a volume of approximately 15 ml/kg of fresh frozen plasma, thereby reducing the risk of compromising a vulnerable cardiovascular system (Franchini 2010); lack of blood group specificity reducing the risk of transfusion-related complications; and finally, viral inactivation may potentially minimize the risk of possible pathogen transmission.
Prothrombin complex concentrate seems to have a faster international normalized ratio correction time compared to fresh frozen plasma, and several studies have suggested a role for prothrombin complex concentrate in the setting of acute neurosurgery by reducing clinical progression of intracerebral haemorrhage (Boulis 1999; Franchini 2010; Steiner 2011).
Why it is important to do this review
Fresh frozen plasma constitutes a well-established procedure worldwide to reverse vitamin K antagonist-induced bleeding disorders (Ansell 2008). However, avoiding blood transfusions represents a possible beneficial effect in terms of possibly reduced mortality and morbidity (Koch 2006a; Koch 2006b; Theusinger 2009). Infusion of viral inactivated non-blood type-specific coagulation factor concentrates in low volumes to reverse oral anticoagulation therapy might offer a potential treatment in people experiencing vitamin K antagonist-induced bleeding complications and people with supranormal INR levels requiring acute surgical intervention. Prothrombin complex concentrate is already part of American and European guidelines for the reversal of acute life-threatening bleeding related to elevated INR (Ansell 2008; Baglin 2006). However, it is important to stress that rapid perioperative reversal of INR is not necessarily associated with a better clinical outcome. Differentiating between therapeutic indications and clinical risk assessment is vital in order to balance the possible benefits (e.g. reduced amount of blood transfusions and avoidance of volume overload, dilutional coagulopathy, pathogen transmission, transfusion-related acute lung injury and the time-consuming process of thawing blood group-specific fresh frozen plasma) and the drawbacks (e.g. inducing life-threatening thrombotic events such as acute myocardial infarction, pulmonary embolism or cerebral venous thromboembolism) with regard to treating an acute bleeding complication or preventing the bleeding complication arising by using exogenous coagulation factors (Warren 2009). More compelling evidence is needed in this area, and the increasing use of prothrombin complex concentrate should be accompanied by a systematic assessment of its potential benefits as well as adverse events. The aim of this review is to assess the evidence that prothrombin complex concentrate is beneficial or harmful for vitamin K antagonist-treated patients undergoing acute surgery compared to placebo, fresh frozen plasma or other haemostatic agents.
We will assess the benefits and harms of prothrombin complex concentrate compared to fresh frozen plasma, other haemostatic agents and placebo in the perioperative setting of acute surgical intervention in bleeding and non-bleeding patients. We will look at various outcomes and predefined subgroups, and will perform sensitivity analyses. We will examine the risks of bias and apply trial sequential analyses (TSA) (Wetterslev 2008) to examine the level of evidence, and will provide a 'risk of bias’ (ROB) table in order to test the quality of the evidence (Guyatt 2008).
Criteria for considering studies for this review
Types of studies
We will include randomized controlled trials (RCTs) irrespective of publication status, date of publication, blinding status, outcomes published, or language. We will contact the investigators and the authors in order to retrieve relevant data. We will include unpublished trials only if trial data and methodological descriptions are either provided in written form or can be retrieved from the study authors. We will also include cluster-randomized trials due to an expected low number of includable trials, but we will exclude cross-over trials and observational studies. We will attempt to adjust the sample size of cluster-randomized trials using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Cochrane Handbook), by using an estimate of intercluster correlation co-efficient (ICC) derived from the trial or from a study of a similar population. We intend to include trials which apply interventional invasive procedures such as endoscopy, interventional radiology and vascular procedures (i.e. embolization, stenting of aneurisms) and less extensive procedures (i.e. nasal balloon tamponade) in this review, to extend the general applicability of the evidence.
Types of participants
We will include people treated with vitamin K antagonist (VKA) undergoing acute surgery or surgical intervention related to bleeding complications arising from VKA treatment. We will also include VKA-treated people with supranormal INR values undergoing acute surgery or surgical intervention due to comorbidity. We will exclude trials including neonates and patients with hereditary bleeding disorders and/or significant liver dysfunction.
Types of interventions
We will include trials on prothrombin complex concentrate (PCC) versus fresh frozen plasma (FFP). We will include trials using any dose of PCC, with any duration of administration and/or additional co-interventions. Furthermore, we will include trials comparing PCC with other haemostatic agents (e.g. vitamin K, recombinant factor VIIa and other plasma derivatives). We will undertake separate subgroup analyses of trials in which PCC is compared to other active interventions or combined with co-interventions:
- PCC versus any comparator;
- PCC versus placebo or no treatment;
- PCC versus fresh frozen plasma;
- PCC versus other haemostatic agents (vitamin K, recombinant factor VIIa or other plasma derivatives or factor-substitution products);
- PCC in combination with other haemostatic agents versus placebo, no treatment or usual treatment with or without haemostatic agents.
Types of outcome measures
Depending on the time scales of the included studies, we plan to run separate analyses for short-, medium- and long-term mortality. The ranges of the different time points will be defined in accordance with the definitions of the included studies and any related clinical considerations.
- Overall mortality. We will use the longest follow-up data from each trial regardless of the period of follow-up.
- Overall 28-day mortality. We will include data provided as 30-day mortality in the same analysis.
- Incidence of perioperative blood transfusions (e.g. avoidance of transfusion) and amount of blood products transfused.
- Complications that are probably related to the intervention, e.g. thrombotic episodes (pulmonary embolism, myocardial infarction, disseminated intravascular coagulation), heparin-induced thrombocytopenia, major immunological and allergic reactions (TRALI), cardiopulmonary overload (TACO), infections and sepsis (e.g. transmission of viral infections).
- Complications during the inpatient stay not specific to the trial intervention, e.g. pneumonia, congestive cardiac failure, respiratory failure and renal failure.
- Number of days in hospital.
- Mean length of stay in the intensive care unit (ICU).
Search methods for identification of studies
We will search the current issue of the Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library); MEDLINE (Ovid SP, 1950 to date); EMBASE (Ovid SP, 1980 to date); International Web of Science (1964 to date); Latin American Caribbean Health Sciences Literature (LILACS via BIREME, 1982 to date); the Chinese Biomedical Literature Database; advanced Google, and Cumulative Index to Nursing & Allied Health Literature (CINAHL, 1980 to date). We will utilize a systematic and sensitive search strategy to identify relevant randomized clinical trials with no language or date restrictions. For our detailed search strategies please see Appendix 1. We will adapt our MEDLINE search strategy for searching in all other databases.
Searching other resources
We will handsearch the reference lists of reviews, randomized and non-randomized studies, and editorials for additional studies. We will contact the main authors of studies and experts in this field to ask for any missed, unreported or ongoing studies. We will contact the pharmaceutical companies for any unpublished trials. We will search for ongoing clinical trials and unpublished studies on the following Internet sites:
Data collection and analysis
Selection of studies
We will assess the reports identified from the described searches and will exclude obviously irrelevant reports. Two authors will independently examine them for eligibility. This process will be without blinding of authors, institution, journal of publication or results. We will resolve disagreements by discussion and if no agreement is reached we will consult a third person. We will provide a detailed description of the search and assessment.
Data extraction and management
Using a data extraction sheet (Appendix 2), we will evaluate each study, enter the data in Review Manager 5 (RevMan 5.2) and check for accuracy. If data in the identified reports are unclear, we will attempt to contact the authors of the original study to invite them to provide further details. Two review authors will independently extract the data, in accordance with Appendix 2. We will resolve disagreements by discussion and if no agreement is reached, we will consult a third person.
Assessment of risk of bias in included studies
Two review authors will independently assess the risk of bias, using the criteria outlined in the Cochrane Handbook. We will resolve disagreements by discussion and if no agreement is reached, we will consult a third person. Each question of validity will be addressed systematically as described by the following:
1) Random sequence generation
Assessment of randomization: the sufficiency of the method in producing two comparable groups prior to intervention.
Grading: ’Low risk’: a truly random process, e.g. random computer number generator, coin tossing or throwing dice; ’High risk’: any non-random process, e.g. date of birth, date of admission by hospital or clinic record number, or by availability of the intervention; or ’Unclear risk’: insufficient information.
2) Allocation concealment
Allocation method prevented the investigators or participants from foreseeing assignment.
Grading: ’Low risk’: central allocation or sealed opaque envelopes; ’High risk’: using open allocation schedule or other unconcealed procedure; or ’Unclear risk’: insufficient information.
Assessment of appropriate blinding of the investigation team and participants: person responsible for participant’s care, participants, and outcome assessor.
Grading: ’Low risk’: we consider blinding as adequate if participants and personnel were kept unaware of intervention allocations after inclusion of participants into the study, and the method of blinding involved a placebo indistinguishable from the intervention, since mortality is an objective outcome; ’High risk’: not double-blinded, categorized as an open-label study, or without use of a placebo indistinguishable from the intervention; ’Unclear risk’: blinding not described.
4) Incomplete outcome data
Completeness of the outcome data including attritions and exclusions.
Grading: ’Low risk’: if the numbers and reasons for drop-outs and withdrawals in the intervention groups were described or if it was specified that there were no drop-outs or withdrawals; ’High risk’: if no description of drop-outs and withdrawals was provided; ’Unclear risk’: if the report gave the impression that there were no drop-outs or withdrawals, but this was not specifically stated.
5) Selective reporting
The possibility of selective outcome reporting.
Grading: ’Low risk’: if the reported outcomes are those prespecified in an available study protocol or, if this is not available, the published report includes all expected outcomes; ’High risk’: if not all prespecified outcomes have been reported, have been reported using non-prespecified subscales, reported incompletely or the report fails to include a key outcome that would have been expected for such a study); ’Unclear risk’: Insufficient information.
6) Other bias
The assessment of any possible sources of bias not addressed in domains 1 to 5.
Grading: ’Low risk’: if the report appears to be free of such biases; ’High risk’: if at least one important bias is present related to study design, early stopping due to some data-dependent process, extreme baseline imbalance, academic bias, claimed fraudulence or other problems; or ’Unclear risk’: insufficient information, or evidence that an identified problem will introduce bias.
With reference to domains 1 to 6 above, we will assess the likely magnitude and direction of the bias and whether we consider it likely to impact on the findings. The impact will be explored through sensitivity analyses. Please see 'Sensitivity analysis' below.
Measures of treatment effect
We will calculate risk ratios (RRs) with 95% confidence intervals (CIs) for dichotomous data (binary outcomes). These will include:
1. Overall mortality. We will use the longest follow-up data from each trial regardless of the period of follow-up.
2. Overall 28-day mortality. We will include data provided as 30-day mortality in the same analysis.
1. Complications that are probably related to the intervention, e.g. thrombotic episodes (pulmonary embolism, myocardial infarction, disseminated intravascular coagulation), major immunological and allergic reactions (TRALI), cardiopulmonary overload (TACO), infections and sepsis (e.g. transmission of viral infections).
2. Complications during the inpatient stay not specific to the trial intervention, e.g. pneumonia, congestive cardiac failure, respiratory failure and renal failure.
We will use the mean difference (MD) if data are continuous and measured in the same way between trials. We will use the standardized mean difference (SMD) to combine trials that measure the same outcome with different scales. These will include:
1. Incidence of blood transfusions (e.g. avoidance of transfusion) and the amount of blood products transfused.
2. Number of days in hospital.
3. Mean length of stay in the intensive care unit (ICU).
Unit of analysis issues
We will exclude cross-over trials from our meta-analyses because of the potential risk of ´carry-over´ of treatment effect in the context of bleeding. However, we will include them in the review and discuss their shortcomings and their findings.
Studies with multiple intervention groups
In studies designed with multiple intervention groups we will combine groups to create a single pairwise comparison (Cochrane Handbook). In trials with two or more prothrombin complex concentrate groups receiving different doses, we will combine data where possible, for the primary and secondary outcomes.
Dealing with missing data
We will contact the authors of trials with missing data in order to retrieve the relevant information. For all included studies we will note levels of attrition and any exclusions. We will conduct a sensitivity analysis exploring the impact of included studies with high levels of missing data. In case of missing data, we will choose ’complete-case analysis’ for our primary outcomes, which excludes from the analysis all participants with the outcome missing. Selective outcome reporting occurs when nonsignificant results are selectively withheld from publication (Chan 2004), and is defined as the selection, on the basis of the results, of a subset of the original variables recorded for inclusion in publication of trials (Hutton 2000). The most important types of selective outcome reporting are: selective omission of outcomes from reports; selective choice of data for an outcome; selective reporting of different analyses using the same data; selective reporting of subsets of the data and selective under-reporting of data (Cochrane Handbook). Statistical methods to detect within-study selective reporting are still in their infancy. We will try to explore for selective outcome reporting by comparing publications with their protocols if the latter are available.
Assessment of heterogeneity
We will explore heterogeneity using the I² statistic and Chi² test. An I² statistic above 50% represents substantial heterogeneity (Higgins 2003). In case of I² > 0 (mortality outcome), we will try to determine the cause of heterogeneity by performing relevant subgroup analyses. We will use the Chi² test to provide an indication of heterogeneity between studies, with P ≤ 0.1 considered significant.
Assessment of reporting biases
Publication bias arises when the dissemination of research findings is influenced by the nature and direction of results (Cochrane Handbook). We will explore the level of publication bias related to the trials included in the review by generating a funnel plot, provided that 10 or more included trials contribute to the outcome (Cochrane Handbook).
Funding bias is related to the possible publication delay or discouragement of undesired results in trials sponsored by the industry (Cochrane Handbook). We will conduct a sensitivity analysis to explore the role of funding.
We will use Review Manger 5 software (RevMan 5.2) in order to perform meta-analyses on pre-stated outcomes from the included trials. If we perform the meta analyses and I² = 0, we will only report the results from the fixed-effect model; in the case of I² > 0 we will report only the results from the random-effects model unless one or two trials contribute more than 60% of the total evidence provided, in which case the random-effects model may be biased. We believe there is little value in using a fixed-effect model in cases of substantial heterogeneity, which we expect would be due to the various factors leading to massive bleeding. We will pool studies only in case of low clinical heterogeneity. When using meta-analysis for combining results from several studies with binary outcomes (i.e. event or no event), adverse side effects may be rare but serious, and hence important (Sutton 2002). Most meta-analytic software does not include trials with ’zero events’ in both arms (intervention versus control) when calculating a risk ratio (RR). Exempting these trials from the calculation of a RR and 95% confidence interval (CI) may lead to overestimation of a treatment effect. The Cochrane Collaboration recommends application of the Peto odds ratio (OR), which is the best method of estimating odds ratios when there are many trials with no events in one or both arms (Cochrane Handbook). However, the Peto method is generally less useful when the trials are small or when treatment effects are large. We will try to conduct a sensitivity analysis by applying the Peto OR if this appears to be a valid option.
Trial sequential analysis
Trial sequential analysis (TSA) is a methodology that combines an information size calculation for meta-analysis with a threshold of statistical significance. Trial sequential analysis is a tool for quantifying the statistical reliability of data in a cumulative meta-analysis, adjusting significance levels for sparse data and repetitive testing on accumulating data. We will conduct trial sequential analysis at least on the primary outcomes (Brok 2009; Pogue 1997; Pogue 1998; Thorlund 2009; Wetterslev 2008) and on the secondary outcomes if the accrued information size is an acceptable fraction of the estimated required information size to allow meaningful analyses (greater than 20). If the actual accrued information size is too low we will provide the required information size given the actual diversity (Wetterslev 2009) and a possible diversity of 25%.
Meta-analysis may result in type I errors due to random errors arising from sparse data or repeated significance testing when updating the meta-analysis with new trials (Brok 2009; Wetterslev 2008). Bias (systematic error) from trials with low methodological quality, outcome measure bias, publication bias, early stopping for benefit and small trial bias may also result in spurious P values (Brok 2009; Cochrane Handbook; Wetterslev 2008).
In a single trial, interim analysis increases the risk of type I errors. To avoid these, group sequential monitoring boundaries are applied to decide whether a trial could be terminated early because of a sufficiently small P value, i.e. the cumulative Z-curve crosses the monitoring boundaries (Lan 1983). Sequential monitoring boundaries can also be applied to meta-analysis, and are called trial sequential monitoring boundaries. In trial sequential analysis the addition of each trial in a cumulative meta-analysis is regarded as an interim meta-analysis and helps to clarify whether additional trials are needed.
The idea in trial sequential analysis is that if the cumulative Z-curve crosses the boundary, a sufficient level of evidence is reached and no further trials may be needed (firm evidence). If the Z-curve does not cross the boundary, then there is insufficient evidence to reach a conclusion. To construct the trial sequential monitoring boundaries the required information size is needed and is calculated as the least number of participants needed in a well-powered single trial (Brok 2009; Pogue 1997; Pogue 1998; TSA User Manual 2011; TSA - Trial Sequential Analysis (computer program); Wetterslev 2008). We will apply trial sequential analysis as it prevents an increase in the risk of type I error with sparse data or multiple updating in a cumulative meta-analysis. Hence, trial sequential analysis provides us with important information in order to estimate the level of evidence of the experimental intervention. Additionally, trial sequential analysis provides us with important information regarding the need for additional trials and their sample size.
We will apply trial sequential monitoring boundaries according to the required diversity-adjusted information size (Wetterslev 2009), based on an a priori 20% risk ratio reduction (RRR), an intervention effect estimated from the trials with a low risk of bias, and a diversity-adjusted required information size estimated from the intervention effect suggested by all the trials, employing α = 0.05 and ß = 0.20 and the diversity found among the included trials. We will use the control event proportion suggested by all the trials, and in case of the actual diversity being zero we will do a TSA challenging a situation where the diversity would be 25%
Subgroup analysis and investigation of heterogeneity
We plan the following subgroup analyses:
- The benefits and harms of prothrombin complex concentrate (PCC) versus fresh frozen plasma (FFP) without other haemostatic agents;
- The benefits and harms of PCC versus FFP and cryoprecipitate;
- The benefits and harms of PCC versus other haemostatic agents (rVIIa, antifibrinolytics, desmopressin, plasma derivatives or other factor-substitution products);
- The benefits and harms of PCC versus FFP in combination with other haemostatic agents;
- The benefits and harms of PCC in combination with other haemostatic agents versus 'standard treatment';
- The benefits and harms of PCC in trials investigating the emergency surgery population (defined as surgery which should be performed within 24 hours after meeting the indication for surgery) requiring acute surgical intervention due to bleeding complications versus trials investigating the emergency surgery population with no bleeding complication requiring acute surgical intervention due to co-morbidity;
- The benefits and harms of PCC in trials investigating the trauma population versus trials investigating the non-trauma population;
- The benefits and harms of PCC in trials investigating the neurosurgical population versus trials investigating the non-neurosurgical population;
- The benefits and harms of PCC in trials investigating the cardiac surgery population versus trials investigating the non-cardiac surgery population;
- The benefits and harms of PCC in trials investigating the paediatric population (age below 18 years, neonates not included) versus trials investigating the adult population;
- The benefits and harms of PCC by comparing the pooled intervention effect in trials with a dose regimen that was higher than the median dose of administered PCC with trials having a dose regimen equal to or smaller than the median dose. This is in order to detect a possible dependency of the estimate of intervention effect on the dose regimen. In case of considerable between-trial heterogeneity, we will apply meta-regression;
- Efficacy and safety of 3-factor PCC versus 4-factor PCC.
If analyses of various subgroups with binary data are significant, we plan to perform a test of interaction by applying the fixed inverse variance method incorporated in RevMan 5.2. Alternatively, we will apply meta-regression if a fixed-effect model is not considered sensible due to considerable between-study variability. We consider P < 0.05 as indicating significant interaction between the PCC effect on mortality and subgroup category (Cochrane Handbook, Chapters 9.6.1 and 9.7). We will also consider applying Q-partitioning for interaction and subgroup difference if appropriate (RevMan 5.2).
We plan the following sensitivity analyses:
- Comparison of estimates of the pooled intervention effect in trials with low risk of bias to estimates from trials with high risk of bias (i.e. trials having at least one inadequate risk of bias component).
- Comparison of estimates of the pooled intervention effect in trials based on different components of risk of bias (random sequence generation, allocation concealment, blinding, completeness of outcome data, selective reporting and 'other bias').
- Comparison of estimates of the pooled intervention effect in trials with high levels of missing data. In case of missing data we will apply ’complete-case analysis’ for primary and secondary outcomes, thereby excluding from the analysis all participants with missing outcome data.
- Examining the role of funding bias by excluding trials that are exclusively sponsored by pharmaceutical and medical devices companies.
- Comparison of estimates of the pooled intervention effects by excluding data from studies only published as abstracts.
- Examining the importance of thromboembolic events when comparing participants with high prior risk of thrombotic events versus others.
We will calculate RRs with 95% CI and decide to apply 'complete-case analysis', if possible, for our sensitivity and subgroup analyses based on our primary outcome measure (mortality).
We thank Dr Karen Hovhannisyan (Trials Search Co-ordinator, Cochrane Anaesthesia Review Group (CARG)) for his assistance in providing our different search strategies. We thank Jane Cracknell (Managing Editor, CARG) for her valuable assistance during the entire process.
We would like to thank Andy Smith (content editor), Marialena Trivella (Statistical editor), Laura Green, Michael Makris and Giancarlo M Liumbruno (peer reviewers) for their help and editorial advice during the preparation of this protocol.
Appendix 1. MEDLINE (Ovid SP) search strategy
1. ((prothrombin adj3 complex) or Beriplex or Octaplex).af.
2. ((randomized controlled trial or controlled clinical trial).pt. or randomized.ab. or placebo.ab. or clinical trials as topic.sh. or randomly.ab. or trial.ti.) not (animals not (humans and animals)).sh.
3. 1 and 2
4. ((anticoagulat* therap* or perioperative) adj5 revers*).af.
5. 3 or 4
Appendix 2. Data extraction form
Study Selection, Quality Assessment & Data Extraction Form
* issue relates to selective reporting when authors may have taken measurements for particular outcomes, but not reported these within the paper(s). Reviewers should contact trialists for information on possible non-reported outcomes & reasons for exclusion from publication. Study should be listed in ‘Studies awaiting assessment’ until clarified. If no clarification is received after three attempts, study should then be excluded.
References to trial
Check other references identified in searches. If there are further references to this trial link the papers now & list below. All references to a trial should be linked under one Study ID in RevMan.
Participants and trial characteristics
see Appendix 2, usually just completed by one reviewer
We recommend you refer to and use the method described by Juni (Juni 2001)
Were withdrawals described? Yes ? No ? not clear ?
References to other trials
Contributions of authors
Conceiving the review: MJ (Mathias Johansen), AW (Anne Wikkelsøe), AA (Arash Afshari) and JL (Jens Lunde)
Designing the review: MJ, AW, AA
Co-ordinating the review: MJ
Undertaking manual searches: MJ, JL
Screening search results: MJ, JL, AA
Organizing retrieval of papers: MJ, JL
Screening retrieved papers against inclusion criteria: MJ, JL
Appraising quality of papers: MJ, JL, AA, AW
Abstracting data from papers: MJ, JL
Writing to authors of papers for additional information: MJ, JL, AA
Providing additional data about papers: MJ, JL, AW
Obtaining and screening data on unpublished studies: MJ, JL, AA
Data management for the review: MJ
Entering data into Review Manager 5 (RevMan 5.2): MJ, JL, AW
RevMan statistical data: AA, AW
Other statistical analysis not using RevMan: AA, JW
Double entry of data: (data entered by person one: MJ ; data entered by person two: JL)
Interpretation of data: MJ, AW, AA, JL, JW
Statistical inferences: AA, AW, JW
Writing the review: MJ
Providing guidance on the review: AA, AW
Securing funding for the review: MJ, AW, AA
Performing previous work that was the foundation of the present study: AW, AA
Guarantor for the review (one author) MJ
Person responsible for reading and checking review before submission MJ
Declarations of interest
Mathias Johansen: none known
Anne Wikkelsø: none known
Jens Lunde: none known
Jørn Wetterslev: none known
Arash Afshari: none known
Sources of support
- Cochrane Anaesthesia Review Group (CARG), Denmark, Not specified.
- Karen Hovhannisyan (CARG), Denmark, Denmark.Technical support and search strategy design
- No sources of support supplied