Types of studies

We will include randomised controlled trials (RCTs), cluster RCTs, and quasi‐RCTs (QRCTs). Quasi‐randomisation is defined as some pseudo‐random method of allocation such as alternation, date of birth, case record number or date of presentation (Higgins 2011). We will include cross‐over studies, if separate data for both time periods are presented. We will only use the data of the first period for analysis to avoid carry‐over effects. We will require full journal publication. Where full journal publication is not available, we will try to obtain data by contacting the trial authors, unless sufficient data for analyses are provided in online clinical trial results, summaries of otherwise unpublished clinical trials, or conference abstracts. QRCTs will be included in order to obtain the full breadth of relevant trials, in particular as we expect to find a small number of RCTs for some of the intervention categories; we are aware of the higher risk of bias in these studies and will account for this in the analysis.

Types of participants

Adult patients aged 18 years and above, suffering from advanced diseases with a high prevalence of breathlessness.

We will include studies if the majority (≥ 50%) of participants meet the following criteria.

• Patients suffering from cancer should have advanced local or metastatic disease (e.g. TNM Classification of Malignant Tumours (TNM) state ≥ T3 or N ≥ 1 or M ≥ 1).

• Patients with severe COPD should have a forced expiratory volume in one second (FEV1) predicted of < 50%.

• Patients with pulmonary hypertension will be included if they reach a WHO class level ≥ III, defined by Barst 2004.

• Patients suffering from CHF should have New York Heart Association (NYHA) stage III or IV.

• Patients with ILD or idiopathic pulmonary fibrosis (IPF): all studies will be included as breathlessness is the predominant symptom and there are hardly any disease specific treatment options.

• Patients with neuromuscular diseases (MND, ALS): all studies will be included as advanced disease is marked by the occurrence of breathlessness.

If groups for the inclusion criteria mentioned above were stratified, we will only include the subgroups of interest. We will document difficult decisions in the review. Sensitivity analysis can assess the impact of these decisions on the review's result. Patients included in the studies can be in any setting. We will exclude studies of patients with any condition not regarded as advanced and life limiting such as acute or chronic asthma, or with pre‐existing diagnosis of acute asthma or acute cardiac condition as a primary cause of breathlessness.

Types of interventions

We will include interventions targeting physical functioning to relieve breathlessness according to the following prespecified categories.

• Physical exercises.

• Neuromuscular electrical stimulation.

• Mobility aids.

If we find interventions of interest that do not fit in the above categories, we will define an additional category 'Other' or add new categories if there is a sufficient number of studies.

The judgement for inclusion will be based on the study authors’ description of the intervention; any deviation from this will be explicitly mentioned.

Interventions may take place in any setting, e.g. outpatient clinic, home, hospital, hospice, general medical practice.

The comparator may be no treatment, placebo, attention control, standard care, or a different kind of therapy. We will categorise the control groups into 'active controls' or 'other' based on the description of the comparison group. We will focus on active controls as comparison group in our primary analysis. Concomitant interventions, especially pharmacological treatment, will be accepted, if administered in the same way in both the control and the treatment groups. If these interventions are suspected to have some relevant influence on our outcomes we will consider this in subgroup analysis.

Types of outcome measures

We anticipate that studies will use a variety of outcome measures. To be included, a study must have any measure of breathlessness. Adverse effects of physical interventions will be measured as absent or present and a narrative description of these effects will be given when reported. We will consider all reliable and validated measures for the following outcomes.

Electronic searches

We will search the following databases from their inception to the present, without date or language restrictions.

• Cochrane Database of Systematic Reviews (CDSR), the Cochrane Library.

• Cochrane Central Register of Controlled Trials (CENTRAL),the Cochrane Library.

• MEDLINE (Ovid).

• Embase (Ovid).

• PsycINFO (Ovid).

• LILACS (Bireme).

• CINAHL (Ebsco).

We will search MEDLINE and Embase using both controlled vocabulary (namely, MeSH in MEDLINE and EMTREE in Embase) and a wide range of free‐text terms. To detect all RCTs we will perform the search on MEDLINE using the Cochrane Highly Sensitive Search Strategy, sensitivity‐maximising version (Higgins 2011).

The search strategy for MEDLINE is in Appendix 1.

Searching other resources

We will search the meta‐register of controlled trials (mRCT) (www.controlled‐trials.com/mrct), clinicaltrials.gov (www.clinicaltrials.gov) and the WHO International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) for ongoing trials. In addition, we will check reference lists of reviews and retrieved articles for additional studies, and we will perform citation searches on key articles. We will contact experts in the field for unpublished and ongoing trials. We will contact study authors where necessary for additional information.

We will perform the search in collaboration with the Information Specialist of the Cochrane Pain, Palliative and Supportive Care Group.

Selection of studies

Two review authors (AB, SR) will independently screen all titles and abstracts retrieved by the search to identify all trials that may be eligible and for which the full paper should be obtained. Independent review authors will eliminate studies that clearly do not satisfy inclusion criteria, and obtain full copies of the remaining studies. Two review authors (AB, SR) will read these studies independently to select relevant studies, and in the event of disagreement or unclear decision to include, we will resolve disagreement with a third author (MM or CB, depending on the topic). We will not anonymise the studies in any way before assessment.

We will include a PRISMA flow chart in the full review which will show the status of identified studies (Moher 2009) as recommended in Part 2, Section 11.2.1 of the Cochrane Handbook (Higgins 2011). We will include studies in the review irrespective of whether measured outcome data are reported in a ‘usable’ way.

Data extraction and management

Two review authors (SR, AB or MM) will independently extract data using a data collection form based on a standard form released by the Cochrane Effective Practice and Organisation of Care Group (EPOC) and check for agreement before entry into Review Manager (RevMan 2014). Where there is disagreement, a third author (CB or SB) will be consulted to resolve differences. We will include information about the following.

Assessment of risk of bias in included studies

Two authors (AB, MM) 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.

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 assessed as high risk of bias.

• 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); high risk of bias (studies that do not conceal allocation (e.g. open list); unclear risk of bias (method not clearly stated).

• 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); high risk of bias (no or incomplete blinding); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved). We will also report if study participants are asked about their expectations of benefit of intervention/control if blinding is not feasible.

• 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 incomplete data as: low risk (< 10% of participants did not complete the study and/or data have been imputed using appropriate methods); high risk of bias (used 'completer' analysis); unclear risk of bias (insufficient information for low/high risk of bias category).

• Selective reporting (checking for reporting bias). We will assess the methods as: low risk of bias (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported); high risk of bias (where not all the study’s prespecified outcomes have been reported; one or more reported primary outcomes were not prespecified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported); unclear risk of bias (insufficient information for low/high risk of bias category).

• Other bias (e.g. 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)).

We will use the Review Manager tool to complete a 'Risk of bias' table (RevMan 2014). Any discrepancy between the two authors will be resolved by discussion involving a third author (CB).

Measures of treatment effect

We will analyse dichotomous outcomes using risk ratios (RRs) with 95% confidence intervals (CIs). We will recategorise any categorical outcomes with more than two categories into two groups. We will analyse continuous data using standardised mean differences (SMDs) with 95% CIs. We will calculate standard deviations, if not reported, using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We plan to report the proportion of participants experiencing any adverse effects of physical interventions, and combine studies using RRs with 95% CI.

Unit of analysis issues

We will reanalyse data, if possible, for cluster trials which have not taken clustering into account in their analysis. We will calculate effective sample sizes and adjusted standard errors using the design effect method. We will try to obtain estimates for intracluster correlation coefficients from study authors or will use external estimates obtained from comparable studies, as recommended by Cochrane guidelines (Higgins 2011). We will document if reanalysis is not feasible.

In studies with more than two arms, we will consistently choose the active control arms in the main analysis, and, if possible, do a sensitivity analysis, in which we will choose the other control arm. We will combine individually randomised controlled trials and cluster RCTs in the same meta‐analyses or harvest plots, but these will be clearly identified (Higgins 2011).

Dealing with missing data

We will contact study authors if missing data on study characteristics or outcome measures precludes study inclusion or limits use of a study at further stages of the review. If studies do not report outcomes based on intention‐to‐treat analyses this will be considered as a source of bias during 'Risk of bias' assessment. We will try to calculate effect measures or CIs wherever possible from available data, if we get no response.

Assessment of heterogeneity

We will assess methodological and clinical heterogeneity with tables documenting the following characteristics of the included studies.

• Intervention components (e.g. physical exercises, neuromuscular electrical stimulation, mobility aids).

• Intervention delivery mechanism (e.g. face‐to‐face, distant).

• Provider characteristics (e.g. nurses, physiotherapists, physicians).

• Setting (e.g. outpatient clinic, hospice, home).

• Patients (e.g. COPD, cancer, fibrosing lung disease).

• Methods (outcome measures, outcome assessment).

For those studies assessing the impacts of a given intervention category on comparable outcomes, thus making pooling through meta‐analysis feasible, we will assess statistical heterogeneity graphically with a forest plot by examining the extent to which CIs overlap, and statistically with the I² statistic. We will consider an I² value greater than 50% to indicate substantial statistical heterogeneity, and will consider it statistically significant if the P value for the Chi² test is < 0.1. We will document statistical heterogeneity but this will not have any direct consequences for meta‐analysis (see below). We will create forest plots and I² calculations using Review Manager 5.3 (RevMan 2014).

Assessment of reporting biases

We will try to minimise publication bias by searching trials registers for projected and registered studies that have never been published. We will contact the authors to get unpublished information if there are such studies registered or some relevant information is missing and can therefore narrow the risk of reporting bias. We will assess the possibility that publication bias affects the review using funnel plots when at least 10 studies are available for meta‐analysis.

Data synthesis

We will attempt to pool all studies within a given intervention category assessing the same outcome by conducting a meta‐analysis using Review Manager 5.3 (RevMan 2014). We will use the random‐effects model due to the expected large heterogeneity in delivery mechanisms, provider characteristics, setting and study population.

We will report results as RRs for dichotomous outcomes and SMDs for continuous outcomes. We will undertake meta‐analysis only if studies are judged to be similar enough to give a clinically meaningful answer. We will provide an outcome table and summarise the results narratively if meta‐analysis is not possible.

In the case of skewed data, we will log transform these data for our analysis or, if that approach is not feasible, summarise them narratively.

Subgroup analysis and investigation of heterogeneity

We will undertake subgroup analysis for the primary outcomes to examine factors that may explain variation in the effectiveness, if numbers are sufficiently large. We will perform stratification as follows.

• Type of intervention.

• Intervention delivery (delivery mechanisms such as face‐to‐face, distant; group, individual; provider characteristics such as nurses, physicians, multiprofessional; setting such as outpatient clinic, home, hospital).

• Patient characteristics (underlying disease, disease stage, age, gender).

• Underlying therapy.