Criteria for considering studies for this review
Types of studies
We will only include reports of randomised controlled trials (RCTs) in this review. This will include randomised cross-over trials and cluster randomised trials. We will consider single and multi-centre studies.
Types of participants
Studies recruiting both malignant and non-malignant participants with no clear distinction between the two groups in the results section
Studies evaluating the effect of a drug administered via any method other than the intra-pleural route
Studies including patients with effusions within a variety of body cavities (e.g. pleural, peritoneal and/or pericardial), where the effect of the treatments in the subgroup of patients with pleural effusions can not be distinguished in the results section
Types of interventions
We will identify studies by comparing the following.
Type of sclerosant.
Mode of administration of sclerosant (thoracoscopic pleurodesis and bedside pleurodesis).
Bedside or thoracoscopic pleurodesis and indwelling pleural catheter insertion.
Techniques used to optimise pleurodesis success rate, namely:
chest drain size;
type of analgesia given;
duration of drainage after instillation of sclerosant;
patient positioning after pleurodesis (for example, patient rotation);
use of intrapleural fibrinolytic.
A thoracoscopic procedure entails drainage of the pleural fluid and direct visualisation of the pleural space and may be performed under general anaesthetic or sedation. Talc poudrage is the technique whereby a sclerosant is instilled into the pleural cavity during a thoracoscopy. Instillation of sclerosant at the bedside through a chest drain is known as a 'bedside pleurodesis' or 'slurry'.
Types of outcome measures
Efficacy of pleurodesis
Definitions of pleurodesis success vary significantly between studies and although current practice would define this by a lack of recurrence of symptoms or need for a repeat pleural intervention to manage the effusion, in some older studies, less clinically relevant definitions may have been used (for example, reaccumulation of effusion on radiology). These studies will still be included in the review and the method used to define pleurodesis will be documented for all studies in the assessment of the risk of bias.
For the purposes of the primary outcome, the following hierarchy of preferences will be used to judge pleurodesis failure (with the highest of these reported by any particularly study to be used):
need for a repeat pleural procedure to manage recurrence of the effusion, or ongoing drainage of pleural fluid from an indwelling pleural catheter (if applicable);
evidence of significant pleural fluid reaccumulation on radiology (for example, chest x-ray or ultrasound);
pleurodesis failure in the opinion of the trial investigators.
Similarly, the time point used to define pleurodesis efficacy will be selected using the following hierarchy of preferences:
> 4-7 months;
> 7- 11 months;
< 2 months;
Patients who die before the time point at which pleurodesis efficacy is being assessed, but were deemed to have had a successful pleurodesis until their death, will be included as a pleurodesis success. Similarly, if they were deemed to have had a pleurodesis failure prior to their death (as judged by any of the above criteria) they will be classified as a pleurodesis failure. If data are not available regarding the efficacy of pleurodesis prior to their death, they will be excluded from the analysis.
Adverse effects and complications due to interventions
Patient reported control of breathlessness, as measured by a valid and reliable scale (for example, visual analogue scale, numeric rating scale or dyspnoea/breathlessness specific multidimensional scale)*
The participants' quality of life and symptom control (including pain), as measured by a valid and reliable scale*
Relative costs of the comparative techniques as reported by the individual trials*
The overall mortality in the short, medium and long term
Duration of inpatient stay in days (both total length of stay and from time of intervention until discharge)*
Patient acceptability of the interventions as judged by a valid scale (for example, visual analogue scale or numeric rating scale)*
* if available
Search methods for identification of studies
To identify studies for inclusion in this review, search strategies were developed for the following databases:
The search strategy can be viewed in Appendix 1.
Searching other resources
We will screen the reference lists from the included studies for additional publications. We will also search the reference lists from relevant chapters in key resources, such as the British Thoracic Society Pleural Disease Guidelines 2010Roberts 2010.
Data collection and analysis
Selection of studies
All titles and abstracts retrieved by the search will be screened for relevance by one author (AC). Potentially eligible studies will be identified and we will obtain the full papers. Two authors (AC and NM) will independently assess each study for inclusion to the review and any disagreement will be resolved through discussion or by a third author (NP).
Data extraction and management
Data from each included study will be extracted independently by two of the authors (AC, NM, NP, RB). Disagreements will be resolved through discussion and referral to a third author. Data collected will include the following.
Publication details including:
title, author(s), date, country and other citations details;
study aim and design.
primary and secondary outcomes;
number of participants randomised.
Participant characteristics including:
Details of the interventions and comparison group including type of intervention, duration, dose, mode of administration and number of doses.
Additional data will be requested by authors as required. Data suitable for pooling will be entered into the Cochrane Collaboration's statistical software, Review Manager 2013, by one author (AC).
Assessment of risk of bias in included studies
This section is taken from the PaPaS template for protocols. We will limit inclusion to studies that are randomised as a minimum.
Two of the review authors (AC, NP, RB, NM) will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion. We will assess the following for each study.
Random sequence generation (checking for possible selection bias)
We will assess the method used to generate the allocation sequence as: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). Studies using a non-random process (e.g. odd or even date of birth; hospital or clinic record number) will be excluded.
Allocation concealment (checking for possible selection bias)
The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated). Studies that do not conceal allocation (e.g. open list) will be excluded.
Blinding of outcome assessment (checking for possible detection bias)
We will assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, e.g. identical tablets; matched in appearance and smell); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved); high risk of bias (study not blinded or no mention of blinding in the methodology).
Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We will assess the methods used to deal with loss to follow up for each of the given studies. Due to the challenges of inevitable missing outcome data given the predictable attrition of patients due to death in the palliative care population, we will take into account whether missing data has been justified, whether the rate is similar in the different treatment arms, whether the treatment being evaluated was felt to have an impact on the degree of missing outcome data and whether an intention to treat analysis has been attempted. We will assess the methods used to deal with incomplete data as: low risk (Rate of missing data is balanced between the treatment arms, seems reasonable and has been justified. Data has been analysed according to the patients randomised treatment allocation. A suitable imputation method may have been used to account for missing data); unclear risk of bias (insufficient information given to allocate trial to 'high' or 'low' risk group); high risk of bias (imbalanced missing outcome data between the treatment arms or missing outcome data felt to be related to the true outcome. Reasons for loss to follow up poorly justified. No attempt at ITT analysis. Inappropriate imputation used).
Selective Outcome Reporting
We will assess the studies for selective outcome reporting using the following criteria: low risk of bias (all outcomes pre-defined and reported, for example in a published protocol, or all clinically relevant and reasonably expected outcomes were reported); uncertain risk of bias (unclear whether all pre-defined and clinically relevant outcomes were reported); high risk of bias (one or more clinically relevant and reasonably expected outcome was not reported and data on these outcomes were likely to have been recorded).
Size of study (checking for possible biases confounded by small size)
We will assess studies as being at low risk of bias (≥ 200 participants per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); high risk of bias (< 50 participants per treatment arm).
Other sources of bias
This section will be used to report other biases, which are detected but do not fit into the above categories (for example, industry bias, academic bias or other methodological flaws that may have caused bias). We will assess the methods used to deal with other sources of bias as: low risk (the trial appears to be free from other potential biases); unclear risk of bias; high risk of bias (other source of bias identified).
Measures of treatment effect
For proportions (dichotomous outcomes), such as pleurodesis efficacy and mortality, we will calculate the risk ratio (RR) with 95% confidence intervals (CIs). For continuous data (such as length of hospital stay and cost) we will estimate the mean difference (MD) with 95% CIs. We will calculate the number needed to treat (NNT) to benefit for efficacy outcomes, and the number needed to harm (NNH) for adverse events.
Ordinal outcome measures (for example, breathlessness scales and quality of life data) will be converted to continuous outcomes as long as the scale is long enough. If different scales are used by the included studies, the standardised mean difference will be used.
Unit of analysis issues
If repeated observations on the same participants have occurred during the trial (for example, pleurodesis success rate at different time points), we will analyse these separately. Only one measure per participant will be used for the primary endpoint (Primary outcomes).
For the purpose of meta-analysis, if a study has multiple doses for a certain substance, we will combine and compare all relevant experimental intervention groups with the combination of all relevant control groups.
For cross over trials, we will analyse data using paired-wise analysis taking into account the cross-over design. We will use the generic inverse variance method.
If meta-analysis is planned containing cluster randomised trials, we will use the generic inverse variance method.
Dealing with missing data
We will attempt to contact the study authors of included studies to clarify any missing data. We will impute the missing standard deviations based on the average standard deviations from the other included studies if standard deviations for mean scores have not been reported and it is not possible to obtain the information from the authors. We will only include data for those participants whose results are known if an intention to treat analysis is not reported by the study. However, we will address the potential impact of this missing data in the risk of bias table.
Assessment of heterogeneity
We will extract data from study reports regarding clinical heterogeneity such as details on intervention and control treatment, participant characteristics and the outcomes evaluated.
We expect a degree of clinical heterogeneity between the included study results because of the different methods which can be used to define pleurodesis failure and the different time points it can be assessed at. We will therefore use the random-effects model for the primary outcome measure and the fixed-effects model for sensitivity analysis.
We will quantify the heterogeneity across studies using the I2 statistic, which will be interpreted taking into account the magnitude and direction of effect as well as the confidence interval. Assessments of whether or not a meta-analysis is appropriate will be made on the basis of clinical rather than statistical heterogeneity.
Assessment of reporting biases
We will perform searches in multiple databases to ensure all potentially eligible studies are identified (Electronic searches). The review authors will be alert to duplicated publication of results when analysing the studies to ensure each participant is only included once in the analysis.
If unpublished studies are identified, efforts will be made to obtain sufficient information in order for them to be included in the analysis. The same applies for data published in abstract format.
In studies published in a language other than English, every effort will be made to obtain a translation of at least the abstract. If sufficient information is available, the study may then be included in the analysis.
We will perform meta-analysis to describe the overall results if the studies are considered clinically similar enough for this to be appropriate. Since we expect some clinical heterogeneity between studies (for example due to different definitions of pleurodesis success and different time points used), we believe that the assumption of a single fixed intervention effect across included studies is unlikely to be valid. Our primary analyses will therefore employ random-effects models. Since pooled effect estimates from random-effects models give relatively more weight to smaller studies, which is often considered undesirable, we will however perform sensitivity analyses using fixed-effect meta-analysis models. Meta-analysis will be performed using the Cochrane Collaboration's statistical software, Review Manager 2013.
For continuous data we will use the MD and 95% CIs. We will use the random-effects model if meta-analysis is performed(as we are expecting clinical heterogeneity). We will perform a check to identify if the data are skewed. If this is the case, the data may be analysed on a log scale.
If cluster randomised trials are included in the analysis, we will use the generic inverse-variance method.
To provide a comprehensive assessment of the relative efficacy of the many available pleurodesis agents, we will present pair wise comparisons of the individual agents where possible. In addition, we will perform a multiple interventions meta-analysis. and compare the findings.
If studies are assessed to be unsuitable for meta-analysis, or should insufficient studies be identified for meta-analysis to be performed, we will present data by means of a narrative synthesis. Convergence between the meta-analysis results and the narrative review will be viewed as an indication of strong evidence of the effect.
The adverse effects reported in the studies will be summarised in a qualitative manner, as there is unlikely to be sufficient data to perform meta-analysis.
Subgroup analysis and investigation of heterogeneity
If sufficient data exists, we will conduct subgroup analyses comparing:
the method by which pleurodesis failure was defined;
the time point at which pleurodesis efficacy was assessed (≤ 6 months and > 6 months after the intervention);
different tumour types;
baseline performance status;
age of participants (young, middle aged and old);
the presence or absence of trapped lung.
We will perform sensitivity analysis according to the methodological quality and robustness of the results where available. The sensitivity analyses will be selected from important elements of the risk of bias tool where studies with high risk of bias are identified.