Criteria for considering studies for this review
Types of studies
We will search for randomized controlled trials (RCTs) irrespective of publication status, date of publication, blinding status or language. We will contact the investigators and the authors to retrieve relevant data. We aim to include unpublished trials only if trial data and methodological descriptions are provided in written form or can be retrieved from the study authors. We will also include quasi-randomized trials because of the expected low number of trials that can be included, but we will exclude cross-over trials and observational studies.
However, two major factors make the conduct of RCTs in this population a difficult task: the large sample size required to document the impact of catheter removal in terms of overall mortality; and the lack of economic interest from the industry in conducting such a trial.
The authors have no knowledge of any existing RCTs concerning this subject and anticipate to find none. We do not plan to include non-randomized studies. Instead, we will provide a description of these studies and their results in an appendix.
Types of participants
This study will focus on patients of all ages with candidaemia who have a CVC in place. We will exclude data from patients with no candidaemia (for example other forms of invasive Candida infections such as Candida peritonitis) and from individuals with no CVC in place. We will only consider patients for whom the information about CVC management is available. We will include patients irrespective of their underlying diseases.
We will search for the following data for each patient entering the study.
Main underlying diseases.
Severity of illness.
CVC data and management.
Data on candidaemia.
Demographic information will include age and sex. The main underlying diseases will include solid organ transplantation, haematopoietic stem cell transplantation, AIDS, diabetes mellitus, solid cancer, and haematological neoplasm. We will record abdominal surgeries performed in the two weeks preceding candidaemia as well as receipt of steroids.
We will define the presence and duration of neutropenia by an absolute neutrophil count ≤ 500 cells/µl in the last 30 days. We will consider neutropenia to have persisted if the neutrophil count did not recover (that is, with increases above 500 cells/µl) in the week following diagnosis of candidaemia.
We will obtain the following variables in order to determine the severity of candidaemia: acute physiology and chronic health evaluation (APACHE II score), stay in the ICU, shock requiring inotropic support, respiratory failure requiring invasive mechanical ventilation, renal failure (serum creatinine ≥ 2 mg/dl), renal failure requiring dialysis, and liver insufficiency (aminotransferases or bilirubins above five or 10 times the upper limit of detection, respectively). These variables will have been collected at the time the index blood culture was obtained.
CVC data will include: short versus long permanence CVC, and time for CVC removal. Both will be considered in relation to the date the blood culture was obtained and to the date antifungal therapy was initiated. The diagnosis of candidaemia will be established when Candida species are recovered from a blood culture taken from a patient with sepsis. Duration of candidaemia and time for CVC removal will be calculated from the day the first positive blood culture for Candida was obtained. We will stratify patients as having candidaemia lasting for: (i) three or less days; (ii) four to seven days; and (iii) more than seven days. We will record the Candida species causing candidaemia.
We will consider candidaemia to be CVC-related if significant growth of Candida species is documented from the catheter tip. This could be determined either by semi-quantitative (> 15 colony forming units (CFUs)/catheter segment) or quantitative (> 103 CFUs/catheter segment catheter) cultures. We will not consider differential time to positivity between blood taken from central lines and peripheral veins for the diagnosis of CVC-related candidaemia since this strategy has just been validated for bacterial infections (Mermel 2001; Mermel 2009).
We will stratify patients according to the antifungal drug they received since some drug classes (for example, echinocandins and polyenes) are known to have antibiofilm activity. We will also collect data on the appropriateness of antibacterial therapy for candidaemic patients with a concomitant bacterial bloodstream infection. Therapy will be considered as appropriate if the prescribed antibacterial drug was shown to be active against the bacteria isolated in the blood culture.
We will record time to death and time for hospital discharge in the case of survivors. For the purpose of survival analysis, patients will be censored at week six after the diagnosis of candidaemia.
Types of interventions
For the purpose of this review we will consider CVC removal as removal or replacement of all central venous lines within seven days of the diagnosis of candidaemia (date at which the positive blood culture for Candida was drawn). This criterion will not apply to CVCs exchanged over a guidewire; we will analyse these cases separately.
We will consider a CVC not removed within seven days after the diagnosis of candidaemia to be a comparison.
Types of outcome measures
Overall mortality. We will use the longest follow-up data from each trial regardless of the period of follow-up*.
Time required for clearance of blood culture for Candida species*.
Frequency of persistent candidaemia (defined as any blood culture that remained positive for Candida species after three days of effective antifungal therapy)*.
Complications probably related to candidaemia (metastatic foci of infection (including endocarditis, endophthalmitis and hepatosplenic candidosis)*.
Complications probably related to the intervention: local suppurative and mechanical complications (e.g. pneumothorax, arterial puncture or bleeding requiring blood transfusion).*
Complications during inpatient stay not specific to the trial intervention (e.g. pneumonia, congestive cardiac failure, respiratory failure, renal failure).
Duration of mechanical ventilation*.
Length of stay in the ICU.*
Length of stay in the hospital*.
* Indicates key outcomes to be included in the 'Summary of findings' table in the review.
Search methods for identification of studies
We will conduct searches to identify all published and unpublished studies evaluating CVC removal in patients with candidaemia. We will not apply any language restrictions; when necessary, we will translate papers in languages other than English. We may contact study authors and drug companies in order to obtain additional data from the selected trials.
We will search the Cochrane Central Register of Controlled Trials (CENTRAL) in The Cochrane Library (Appendix 1); MEDLINE (interface PubMed) (1966 to date) (Appendix 2); EMBASE (1966 to date) (Appendix 3); LILACS (1982 to date) (Appendix 4); BIOSIS (1999 to date) (Appendix 5); ISI Web of Knowledge (1945 to date) (Appendix 6); and SCOPUS (1960 to date) (Appendix 7). We will combine the strategies described in Section 6.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to search for RCTs in MEDLINE and EMBASE. We will check the reference lists of all retrieved primary studies for additional relevant studies. Additionally, we will check all references of relevant reviews, meta-analyses, society guidelines, and commentaries identified both in PubMed and EMBASE.
Searching other resources
We will handsearch the reference lists of reviews, randomized and non-randomized studies and editorials to locate 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 try to contact pharmaceutical companies to ask about any unpublished trials, and we will search for ongoing clinical trials and unpublished studies on the following Internet sites.
Current Controlled Trials (http://www.controlled-trials.com)
Data collection and analysis
We will use the standard methods of the Cochrane Anaesthesia Review Group (CARG) to identify studies and to assess the methodological quality of eligible trials. We will use the Review Manager statistical package (RevMan 2012) provided by The Cochrane Collaboration to analyse the data. We will consider the frequency of autopsy rate as well as frequency of daily blood culture in the five days following candidaemia and the percentage of patients excluded after screening for the purpose of quality evaluation.
Selection of studies
We will search for RCTs and quasi-RCTs involving adult patients with candidaemia and in which patients were randomized for CVC removal (the intervention under study). As already mentioned, we will select trials irrespective of their original language.
Two review authors will independently read all the abstracts in the records retrieved by electronic search to identify eligible publications. They will select studies to be reviewed according to prespecified inclusion criteria. This process will be performed without blinding of authors, institution, journal of publication or results. We will resolve disagreements by discussion, and if no agreement can be found, we may consult a third independent person.
We will provide a detailed description of this search and assessment in the form of a PRISMA flow chart in the review.
Data extraction and management
We will assess the quality of eligible trials using the criteria described by the Cochrane Effective Practice and Organisation of Care Group (EPOC) (Reeves 2008). Data extraction will be completed independently by two authors using a data extraction sheet developed for the purposes of this review (Appendix 8). We will conduct an individual patient data (IPD) meta-analysis in a subgroup of trials evaluating specific outcomes in the more homogeneous populations described below.
For each of the trials we will record the following data.
(A) Year of publication, country of origin and source of study funding.
(B) Details of participants including demographic characteristics and criteria for inclusion.
(C) Details of the type of intervention.
(D) Details of the outcomes reported, including method of assessment and time intervals.
Individual patient data (IPD)
We will attempt to contact the investigators of the selected trials by email or telephone to invite them to contribute IPD. In the review we will include data from studies in which IPD are not available. In such cases, we will obtain aggregate data and we will combine these with IPD.
Assessment of risk of bias in included studies
Two review authors will independently assess the risk of bias without blinding using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve disagreements by discussion, and if no agreement is found, we may consult a third person. Each domain will be assessed systematically as described by the following.
1) Random sequence generation
2) Allocation concealment
3) Blinding of participants and personnel
4) Blinding of outcome assessor
5) Incomplete outcome data
7) Other bias
With reference to domains 1 to 6 above, we will assess the likely magnitude and direction of the bias and whether we may consider it likely that it will impact on our findings. We will assess the impact of bias in the sensitivity analyses.
Measures of treatment effect
We will calculate the risk ratios (RRs) with 95% confidence intervals (CIs) for dichotomous data (binary outcome).
We will calculate the mean difference (MD) with 95% CIs for continuous data if they are measured the same way. To combine trials which measure the same outcome but in different ways we will measure the standardized mean difference (SMD).
Unit of analysis issues
Cluster-randomization: We will exclude any cluster-randomized trials as factors related to clustering may contribute to outcome.
Multiple intervention groups: In studies with multiple intervention groups we will combine groups to create a single pair-wise comparison (Higgins 2011).
Unit of analysis issues related to cross-over trials, reoccurring events, repeated observations, multiple treatment attempts and interventions on multiple body parts are considered not relevant with this intervention and outcome.
When meta-analysis is used in combining results from several studies with binary outcomes (i.e. event or no event), adverse effects may be rare, but serious, and hence important (Sutton 2002). Most meta-analytical software does not include trials with 'zero event' in both arms (intervention versus control) when calculating RR. Exempting these trials from the calculation of RR and 95% CI may lead to overestimation of the treatment effect. The Cochrane Collaboration recommends application of the Peto odds ratio (OR), which is the best method of estimating OR when many trials with no event in one or both arms are included (Higgins 2011). However, the Peto method is generally less useful when the trials are small, or when treatment effects are large. We plan to conduct a sensitivity analysis by applying the Peto OR if this sensitivity analysis is seen as a valid option.
In a single trial, interim analysis increases the risk of type I errors. To avoid type I errors, group sequential monitoring boundaries (Lan 1983) are applied to reveal whether a trial could be terminated early because of a sufficiently small P value, that is, the cumulative z-curve crosses the monitoring boundaries. Sequential monitoring boundaries, called trial sequential monitoring boundaries, can be applied to meta-analysis as well.
In trial sequential analysis (TSA), the addition of each trial into a cumulative meta-analysis is regarded as an interim meta-analysis and helps the investigator to decide whether additional trials are needed. The idea behind TSA is that if the cumulative z-curve crosses the boundary, a sufficient level of evidence is reached, and no further trials are needed. If the z-curve does not cross the boundary, then evidence is insufficient to allow investigators to reach a conclusion. To construct the trial sequential monitoring boundaries, the information size is required and is calculated as the least number of participants needed in a well powered single trial (Brok 2008; Pogue 1997; Pogue 1998; Wetterslev 2008; Wetterslev 2009).
We will apply TSA (TSA 2010) because this prevents an increase in the risk of type I error (< 5%) due to potential multiple updating and sparse data in a cumulative meta-analysis and provides us with important information to allow us to estimate the level of evidence for the experimental intervention. Additionally, TSA provides us with important information regarding the need for additional trials and the required information size. We want to perform TSA in anticipation of an intervention effect as indicated by the trials included in the traditional meta-analysis, or even the intervention effect suggested by the upper confidence limit from the intervention effect estimate found in the traditional meta-analysis, to cover any uncertainty displayed by the present data.
We aim to calculate the diversity-adjusted required information size using the pooled variance from the traditional meta-analysis (Turner 2013; Wetterslev 2009), as well as the control event proportion from the meta-analysis of the included trials.
Dealing with missing data
We will contact the corresponding author of all studies with missing data in an attempt to retrieve the relevant data. For all included studies, we will note number of exclusions and whether they are accounted for and assess risk of attrition bias. In case of missing data, we will choose a 'complete case analysis' for our primary outcome, which simply excludes all participants with the outcome missing from the analysis.
Assessment of heterogeneity
We will assess clinical heterogeneity by examining the types of participants, interventions and outcomes in each study. As a preliminary assessment of heterogeneity, we will examine statistical heterogeneity between the summary statistics of different studies by checking the usual statistical test where P values will be obtained by comparing the distribution of the Chi2 statistic. We will take care in the interpretation of the Chi2 statistical test since this has limited power in the (common) situation in which trials have a small sample size or are few in number. We will also assess statistical heterogeneity with the I2 statistic thereby estimating the percentage of total variance across studies that is due to heterogeneity rather than chance (Higgins 2002). We will consider a value of greater than 40% as definitely considerable if it is also significant. In combined analysis of IPD and abstracted data, as well as sensitivity analysis with IPD data only, covariates and random study effect will be used to attempt to explain between-study heterogeneity.
Assessment of reporting biases
Selective outcome reporting occurs when non-significant results are selectively withheld from publication (Chan 2004). It is defined as the selection, on the basis of results, of a subset of the original variables recorded for inclusion in publication of trials (Hutton 2000). We will check publications against their protocols or official registrations of trials when available, in an attempt to detect possible selective outcome reporting.
Publication bias arises when the dissemination of research findings is influenced by the nature and direction of results (Higgins 2011).
We will evaluate the level of publication bias related to the included trials by providing a funnel plot. For studies with binary outcomes, we will apply the test proposed in Rucker 2008. This test has the advantage of including trials with no events.
If the number of included trials does not exceed 10, we will not carry out these tests, as suggested by the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
Funding bias is related to the possible delay or discouragement to publish undesired results in trials sponsored by the industry (Higgins 2011). To explore the role of funding, we will conduct a sensitivity analysis based on our primary endpoint.
We will perform the analysis using Review Manager software (RevMan 2012) and other software if needed. As a general rule, we will use a random-effects model since we do not expect an identical treatment effect across studies, and we intend to draw conclusions for the general population rather than only the included studies. We will compare outcomes across trials and treatment regimens to assess clinical heterogeneity and compare patient populations. Comparisons between health outcomes will be restricted by the different measurement tools used and the method of reporting in the included trials.
Subgroup analysis and investigation of heterogeneity
We will perform subgroup analyses for subgroups of participants and for subgroups of the intervention with the variables as listed before (see Types of participants).
We will perform sensitivity analyses of trials with low risk of bias versus high risk of bias. If evidence of small-study effects is observed, we will also perform sensitivity analyses. We also plan to test the robustness of the results by repeating the analysis using different measures of effect size (for example, RD and OR) and different statistical models (fixed-effect and random-effects models).
Summary of findings
We will use the principles of the GRADE system (Guyatt 2008) to assess the quality of the body of evidence associated with specific outcomes (overall mortality, duration of candidaemia, frequency of persistent candidaemia, incidence of metastatic infection, local suppurative/mechanical complications, length of hospital/ICU stay and species-related mortality) in our review and construct a 'Summary of findings' (SoF) table using the GRADE software. The GRADE approach appraises the quality of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed. The quality of a body of evidence takes into consideration within-study risk of bias (methodologic quality), the directness of the evidence, heterogeneity of the data, precision of effect estimates and risk of publication bias.