Selection criteria
A sample search strategy, for the clinical effectiveness review, for MEDLINE is provided in Appendix 1.
Study design
Systematic reviews will be included in order to obtain an overview of the existing evidence base. RCTs will be included with no restrictions on the type of RCT (for example parallel, cross-over). In view of the steady deterioration in the health of patients with severe COPD, however, it seems unlikely that cross-over studies will be a suitable method to make unbiased comparisons of the long-term efficacy of home NIV. All observational evidence will be obtained, whether controlled or uncontrolled, in order to gain an overview of existing observational evidence. Uncontrolled observational studies will be used where primary outcomes are not reported in the control studies, or, where uncontrolled studies have longer follow-up for these outcomes.
Patient group
The patient group will be adult patients with stable end-stage COPD plus chronic hypercapnic respiratory failure, who have required assisted ventilation (whether invasive or non-invasive) during an exacerbation or who are hypercapnic or acidotic on LTOT, providing they do not require treatment in hospital. The criteria for specifying the population are broad, to include any adult patients with COPD and hypercapnic respiratory failure, however defined, and inclusion will not be restricted by disease severity. Where a study contains a mixed population, the study will be included, but inclusion into analysis will only be possible where data are available separately for the relevant population or if the majority of the population are relevant. In the latter case, such a study’s effect on summary data will be investigated by sensitivity analyses.
Technology
Studies of any form of NIV will be included, whether continuous or intermediate, added to (any form of) standard care. Previous research has shown that patients in acute settings show improvement after four hours [14], however, study inclusion will not be restricted by length of daily use.
Comparators/control
For controlled studies
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a)
Any form of standard care with no NIV; it is noted that both the setting and the nature of standard care in the absence of treatment with NIV may be different to that of treatment with NIV; such differences will not affect inclusion/exclusion decisions, but will be noted and commented upon and considered in the analyses.
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b)
Studies comparing alternative methods of NIV will also be included. The main difference is likely to be whether NIV is set at pressure or volume controlled. Other differences include mask type and number of hours of use per day.
Setting
Home or wider non-hospital setting, operationally this equates to a non-hospital environment.
Outcome
Studies will be included if they contain any outcomes related to patient wellbeing, healthcare service utilisation and/or patient carers. Based primarily on the need to inform an economic model, we consider the main outcomes for the review to be:
Primary outcomes
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survival
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QoL with validated questionnaires for patient and carer (for example EQ5D, SF-36, St George’s Respiratory Questionnaire)
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exacerbations (and requirements for associated medication)
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hospitalisations
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Accident and Emergency admissions
Secondary outcomes
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other healthcare resource use (for example primary care, training)
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lung function (for example, forced expiratory volume in one second (FEV1), forced vital capacity (FVC))
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blood gases (for example, partial pressure of carbon dioxide in arterial blood (PaCO2))
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dyspnoea
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(serious) adverse events (for example, barotrauma, pneumonia, nasal skin lesions)
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other patient- or carer-related outcomes such as quality of sleep, activities of daily living and acceptability
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adherence/compliance rates
Data extraction
Data extraction will be conducted independently by two reviewers using a standardised extraction form. Disagreements will be resolved through discussion or referral to a third reviewer. For each study, the data required on (but not limited to) the following will be sought:
Study characteristics
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country of origin
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study design
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setting
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sample size
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length of follow-up
Population
Intervention/comparator
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NIV versus standard care or NIV versus alternative NIV
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details of standard care (including additional oxygen therapy)
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type of NIV equipment; pressure or volume controlled
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length of nocturnal/daytime NIV
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patient training/education provided
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run-in period (duration/setting)
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patient adherence/compliance (how assessed/reported)
Results
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completeness of follow-up
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outcome measures
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statistical methods employed
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findings
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effect sizes and associated uncertainty
Quality assessment
Data will be extracted to allow quality assessment of the included studies. Study quality will be assessed using tools specific to a given study design. For systematic reviews, the AMSTAR checklist will be used [15]. The risk of bias tool from the Cochrane Handbook will be used for RCTs [16]. Should cross-over trials be included, then additional areas of risk of bias will need to be assessed. These relate to: (i) whether the cross-over design is suitable; (ii) whether there is a carry-over effect; (iii) whether only first-period data are available; (iv) appropriate statistical analysis; and (v) comparability of results with those from parallel-group trials [17].
For observational studies, the guidelines outlined in Chapter 13 of the Cochrane Handbook will be followed [18]. For controlled observational studies the domains in the risk of bias tool for RCTs can be used as a minimum assessment (accepting that the studies are not randomised). The most relevant criteria for assessment in this area are likely to relate to how the groups were selected, differences in patient characteristics, loss to follow-up and biases and confounding in outcome assessment.
For uncontrolled observational studies a tailored assessment tool will be developed for this review based on existing tools (such as the Downs and Black instrument [19] or the Newcastle Ottawa scale [20]). Criteria such as a clear description of population characteristics, use of validated outcome measures and reporting of length and loss to follow-up are likely to be relevant.
In addition to methodological criteria listed above, the GRADE framework [21] will be used to consider inconsistency between studies, precision of results, likelihood of publication bias and applicability of results to population(s) of interest.
Analysis
Narrative synthesis of evidence will be undertaken for all included studies. Results are likely to be presented using a number of different outcome statistics, for example, mean difference, relative risk, hazard ratio and so on. This may be the case even for the same outcome, for example, admissions to hospital could be reported as mean number of admissions per patient or total number of admissions. Survival could be reported as time-to-event data or as relative risk. Time points of reporting are also likely to vary across studies. The relevance of short-term outcome assessment is often related to underlying population risk for the outcome in question. For example, patients discharged from hospital after intensive emergency treatment for an exacerbation of their COPD are at higher risk of a recurrent exacerbation in the immediate aftermath (for example three months) than patients who have been stable without a severe exacerbation for many months. Where appropriate, meta-analytic methods will be employed to combine data reported by the same outcome statistic across the same, or very similar time points; summary statistics will most likely be pooled relative risk for dichotomous outcomes, pooled mean difference for continuous outcomes or pooled hazard ratios. This may involve conversion of different statistics into a single, consistent measure, where appropriate assumptions are met, for example by using the method of Parmar to obtain hazard ratios from dichotomous data [22]. Standardised mean differences will be considered if the same outcome is measured using different assessment tools. Final choice of summary statistic and method of meta-analysis will be guided by the considerations outlined in Chapter 9 of the Cochrane Handbook[23]. Assessment of clinical and methodological heterogeneity will be used to determine whether a fixed or random-effects model is the most appropriate, rather than relying on the tests of heterogeneity from a fixed-effect model to make such a decision [24]. The I2 statistic (which gives the percentage of the total variability in the data due to between-study heterogeneity) and the tau-squared statistic (which gives an estimate of the between-study variance) will be reported where appropriate. Evidence from RCTs and observational studies will not be quantitatively combined, but presented separately.
Consideration may need to be given on whether to incorporate cross-over trials into any meta-analyses. Should cross-over trials be included in a meta-analysis then separate analyses for parallel and cross-over studies will also be presented [17].
For each meta-analysis containing 10 or more studies, the likelihood of publication bias will be investigated through the construction of funnel plots and appropriate statistical tests for small-study effects (such as the Peters Test [25]); that is, the tendency for smaller studies to provide more positive findings. It is well recognised that, especially where heterogeneity exists, publication bias may be one of a number of reasons for any small-study effects identified. The restriction of 10 studies is due to the low power of identifying small-study effects with few studies [16]. Where studies have reported time-to-event analyses, meta-analysis using the extracted hazard ratios and their variances will be undertaken, if possible.
The potential for indirect comparisons/multiple treatment comparisons will be explored, for example if there are RCTs comparing different types of NIV interventions respectively, but with a common comparator (for example, NIV1 versus standard care and NIV2 versus standard care). A number of key assumptions would have to be met, including that of homogeneity and exchangeability of participants between trials [26]. The similarity of trial and population characteristics within and between trials will therefore be assessed qualitatively and statistically; however, if the trials are small there will be limited power to assess the statistical inconsistency of any direct and indirect comparisons. If such comparisons are deemed possible, a Bayesian approach, to take into account parameter uncertainty and allow for probability statements and ranking of treatment modalities, will be used. It is likely that vague priors will need to be used and sensitivity to variation in these will be investigated.
Subgroup analysis
As NIV is becoming easier and cheaper to use in practice, knowledge about how and when to use it, as well as in whom it is most effective, becomes of key clinical and budgetary significance. To aid this and to further assist economic model parameterisation (see below) a priori data analysis of relevant subgroups will be undertaken where deemed appropriate. Where data allows, such analysis could include grouping by clinically perceived effect modifiers such as type of ventilation (for example pressures), patient interface (face/nasal mask), number of hours of use per day of NIV (where there are clear differences in trial protocols), patients on/not on LTOT and severity of disease (including frequent versus non-frequent exacerbators). Severity of disease may not always be well described, but where possible populations will be identified according to, for example, the GOLD criteria (2011) [4] and patients classified as ‘very severe’ may be compared to patients of other grades of severity (‘mild’, ‘moderate’, ‘severe’). Sensitivity analysis may be undertaken where, for example, studies contained a mixed population of those relevant and not relevant to the project. We are unlikely to assess the robustness of any meta-analysis conclusions to varying study quality, unless a clear difference in methodological quality is identified between groups of included studies.