Types of studies

We will include randomised controlled trials (RCTs) and controlled clinical trials (CCTs) that examine inpatient specialist palliative care. We will include randomised trials, non‐randomised trials, controlled before‐and‐after studies, interrupted time series studies and repeated measures studies as recommended by the Cochrane Effective Practice and Organisation of Care (EPOC) Group (Cochrane EPOC 2017). Inclusion of these non‐randomised studies is important because of the limited number of RCTs in palliative and end‐of‐life care (Rinck 1997), as well as their often restrictive selection criteria. To minimise cross‐contamination, we will only include cluster‐unit randomised studies. We will use the list of study design features given in the Cochrane Handbook for Systematic Reviews of Interventions to identify the characteristics of non‐randomised studies in order to include all eligible studies (Higgins 2011a). For controlled before‐and‐after studies there needs to be at least two intervention sites and two control sites, contemporaneous data collection both before and after the intervention, and comparable sites as comparators. For interrupted time series, there needs to be a clearly defined point in time when the intervention occurred and at least three data points before and three after the intervention. We recognise that heterogeneity will be greater in a systematic review of non‐randomised studies than in a systematic review of randomised trials. Therefore, we will consider very carefully the likely extent of heterogeneity between included studies when deciding whether to pool findings quantitatively (i.e. by meta‐analysis). We expect pooling of effect estimates from non‐randomised studies to be the exception, rather than the rule. We will use established approaches to include and analyse non‐randomised studies following Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).

We will examine both effectiveness and cost‐effectiveness components. Although the number of RCTs in palliative and end‐of‐life care is steadily increasing (Rinck 1997), they remain few in number. Non‐randomised studies can provide important understanding on the effectiveness of palliative care services (Higginson 2003), but only with careful attention paid to the likelihood of bias (Field 2004; Strobe 2001). In order to assess whether non‐randomised studies are susceptible to confounding bias, we will use the Risk of Bias in Non‐randomised Studies ‐ of Interventions (ROBINS‐I) assessment tool to determine whether important confounding factors were measured and adjusted for. Important confounding factors in non‐randomised palliative care studies include severity of illness, prognosis, symptom burden, preferences for life‐sustaining treatment, financial resources and social support (Starks 2009). Where we identify additional confounders, we will include them in our assessment.

All studies must evaluate effectiveness regarding one of the stated primary or secondary outcomes stipulated for this review. In the economic component of the review, studies to be included are those that are conducted alongside (or as part of) the main effectiveness trial and ones that also meet the eligibility criteria for the effectiveness component. Full economic evaluation (i.e. cost‐effectiveness analyses, cost‐utility analyses, cost‐benefit analyses); partial economic evaluations (i.e. cost analyses, cost‐description studies, cost‐outcome descriptions); and studies that report more limited information, such as estimates of resource use or costs associated with service use, will be eligible for inclusion in the review.

Types of participants

• Adult (≥ 18 years) patients admitted to an acute hospital for > 24 hours and those in receipt of inpatient specialist palliative care while an inpatient in an acute hospital:

  • these patients will be diagnosed with advanced, life‐limiting or life‐threatening illness (malignant or non‐malignant), which is likely to compromise the patient's quality of life in some way;

  • diseases and health‐related conditions included (with the corresponding International Classification of Diseases (ICD‐10)) are malignant neoplasms (ICD‐10 codes: C00‐C97) and non‐malignant and other health‐related conditions, specifically: heart disease, including cerebrovascular disease (ICD‐10 codes: I00‐I52, I60‐69), renal disease (ICD‐10 codes: N17, N18, N28, I12, I13), liver disease (ICD‐10 codes: K70‐K77), respiratory disease (ICD‐10 codes: J06‐J18, J20‐22, J40‐47, J96), neurodegenerative disease (Huntington’s disease (ICD‐10 code: G10), Parkinson's disease (ICD‐10 code: G20), multiple sclerosis (ICD‐10 code: G35), motor neuron disease (ICD‐10 code: G12.2)), multi‐system degeneration (ICD‐10 code: G90.3), progressive supranuclear ophthalmoplegia (ICD‐10 code: G23.1), Alzheimer’s dementia and senility (ICD‐10 codes: F01, F03, G20, R54), and HIV/AIDS (ICD‐10 codes: B20‐B24));

• Unpaid caregivers who have received a pre‐bereavement intervention from one or more specialist palliative care staff in order to manage or alleviate bereavement‐related problems prior to the death of the inpatient:

  • unpaid caregivers are likely to be family, friends or significant others associated with the patient (Payne 2010a; Payne 2010b).

Types of interventions

Inpatient specialist palliative care varies between settings and countries. In order to allow for these differences, inpatient specialist palliative care will include care for patients with an advanced, life‐limiting or life‐threatening illness that is likely to compromise the patient’s quality of life in some way with or without pre‐bereavement care for unpaid caregivers (provided while the patient is alive and in hospital to either the unpaid caregiver alone or together with the patient) (Higginson 2003). This may include but not be limited to interventions that have been labelled as "palliative care, generic palliative care, hospice care or specialist palliative care". The intervention must be aiming to address the primary outcome of this review or a secondary outcome. It must also be delivered by a specialist palliative care team or by a "specialist palliative care", "palliative care" or "hospice outreach" staff member (but not a generalist palliative care member, as defined in Shipman 2008).

We will include studies of inpatient specialist palliative care compared with usual care. Usual care is defined as inpatient hospital care without any specialist palliative care input (e.g. oncological care only), community care (e.g. primary or specialist care provided in the patient’s place of residence) or hospice care provided outside of the hospital setting. When usual care is compared with specialist palliative care (plus or minus usual care), we will extract descriptive data on what is involved in each intervention. Detailing these items will help address different implications regarding associated cost‐effectiveness and costs in studies with various study designs and diverse specialist palliative care and usual care interventions.

Similar to a Cochrane Review that examined palliative care (Gomes 2013), we will exclude trials that evaluate inpatient specialist palliative care practitioners’ provision of only a biomedical component of palliative care (e.g. oxygen therapy) as this does not encompass the holistic nature of palliative care assessment or treatment. Focusing solely on a biomedical component may also counteract against the 'protective' nature of inpatient specialist palliative care regarding unnecessary or aggressive medical treatment. In addition, in order to limit the size of this review and heterogeneity, we will exclude specialist palliative care delivered to patients by outreach hospital services or within hospital outpatient services. We will include specialist palliative care provided to unpaid caregivers in hospital settings and/or hospital outpatients. This is because unpaid caregivers are likely to be seen as outpatients or in treatment rooms by hospital staff in the hospital to address pre‐bereavement outcomes. A Cochrane Review that examined the effectiveness and cost‐effectiveness of palliative care has been limited by the heterogeneity of both palliative care interventions and 'usual care' (Gomes 2013). Limiting our review in this way will help limit heterogeneity.

Types of outcome measures

We have developed the primary and secondary outcomes for this review from previous reviews regarding the effectiveness of palliative care (Gomes 2013; Gysels 2004; Higginson 2003; Higginson 2010). They reflect the multi‐component nature of palliative care and the provision of both direct (e.g. face‐to‐face delivery of patient care) and indirect patient care (e.g. concerning practitioners' prescribing rationale), and care for unpaid caregivers while the inpatient is still alive. We have chosen to measure pain as our primary outcome rather than quality of life. Research has shown that conducting meta‐analysis on data from instruments that do not measure the same underlying constructs or ones that differ substantially due to responsiveness (as is possible for patient‐reported quality of life instruments) may be problematic, leading to between‐study heterogeneity and biased meta‐analysis (Puhan 2006). Pain control is a top priority for many potential palliative care patients and their unpaid caregivers in many countries (Bausewein 2013), and can be assessed by either the patient or by a proxy i.e. a healthcare clinician or an unpaid caregiver. The use of pain as the primary outcome incorporates a patient‐level clinical outcome as central to the review.

Electronic searches

We will identify studies by searching the databases listed below, using a combination of key terms and MeSH terms:

• Cochrane Library: (Cochrane Central Register of Controlled Trials (CENTRAL); Cochrane Database of Systematic Reviews (CDSR); Database of Abstracts of Reviews of Effects (DARE); Health Technology Assessment (HTA)), current issue of each database;

• MEDLINE & MEDLINE‐in‐Process (OVID), 1947 to present;

• Embase (OVID), 1974 to present;

• CINAHL (EBSCO),1981 to present;

• PsycINFO (OVID), 1806 to present;

• CareSearch, Australian Government's Department of Health and Ageing (http://www.caresearch.com.au/) (from inception to present).

We will also search the following health economic databases to identify further studies:

• National Health Service Economic Evaluation Database (NHS EED), current issue;

• European Network of Health Economics Evaluation Databases (EURONHEED), 1980 to present.

We will modify the MEDLINE search strategy for use in other databases (Appendix 2).

Searching other resources

We will search clinicaltrials.gov (www.clinicaltrials.gov) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (http://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 for additional information where necessary.

Selection of studies

Two review authors will independently screen all titles and abstracts identified in our electronic searches. If, after reading the abstract, doubt persists regarding the eligibility of the study, we will retrieve the full‐text articles for further assessment and again two review authors will independently assess these full‐text articles. A third review author will adjudicate any discrepancies between the two authors’ assessment of eligibility. We will resolve any disagreements by discussion and consensus. We plan to illustrate our study selection process using a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow diagram (Liberati 2009), as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).

Data extraction and management

Two review authors will independently extract data from all included studies using a preliminary data extraction form for the review (Appendix 3) that will be further developed for economic evaluation based on the format and guidelines used to produce structured abstracts of economic evaluations for inclusion in the NHS EED. We will enter data into Review Manager (RevMan) (RevMan 2014). We will resolve any disagreements by discussion and consensus with a third review author. It is likely that the review will include studies by the review authors. In this case these review authors will not be involved in the data extraction or assessments of these studies. The data extraction form has been used previously for a review on the effectiveness of home palliative care (Gomes 2013). We have adapted the form for this review regarding inpatient specialist palliative care. Drawing on an existing data extraction form enables future work comparing the effectiveness and cost‐effectiveness of specialist palliative care across care settings.

We will collate multiple reports of the same study, so that each study rather than each report is the unit of interest in the review. We will collect characteristics of the included studies in sufficient detail to populate a 'Characteristics of included studies' table in the full review.

Assessment of risk of bias in included studies

Two review authors will independently assess risk of bias for each included study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Chapter 12, Schunemann 2011), with any disagreements resolved by discussion. We will complete a 'Risk of bias' table for each included study using the 'Risk of bias' tool for randomised controlled studies and ROBINS‐I tool for non‐randomised studies in RevMan (RevMan 2014).

We will assess the following for each included 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); or unclear risk of bias (method used to generate sequence not clearly stated). We will exclude studies that use a non‐random process (e.g. odd or even date of birth; hospital or clinic record number).

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

• Selective reporting (checking for reporting bias). We will assess whether primary and secondary outcome measures were pre‐specified and whether these were consistent with those reported. We will assess the risk of bias as per the Cochrane Handbook for Systematic Reviews of Interventions (Chapter 8, Higgins 2011b).

• 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 or used ‘baseline observation carried forward’ analysis); unclear risk of bias (used 'last observation carried forward' analysis); or high risk of bias (used 'completer' analysis).

• 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); or high risk of bias (< 50 participants per treatment arm).

We will classify health economics studies per the design of the health economic study (e.g. full economic evaluation, partial economic evaluation) and the design of the study generating the effectiveness data of the health economic study (e.g. a single study design, a synthesis of several studies). For full economic evaluations, we will assess the risk of bias in results of the single effectiveness study on which the full economic evaluation study is based and methodological quality of the full economic evaluation study. We will use as checklists the BMJ Checklist for authors and peer reviewers of economic submissions (Drummond 1996), and the Consensus on Health Economic Criteria (CHEC) list for assessment of methodological quality of economic evaluations (Evers 2005). For assessment of the quality of relevant economic modelling studies we will use tools such as the Consolidated Health Economic Evaluation Reporting Standards (CHEERS) statement (Husereau 2013), and the Quality Appraisal Checklist for Economic Evaluations (NICE 2012), supplemented by the Philips Checklist (Philips 2004).

Cochrane guidance provides scope for assessing the risk of bias based on the likelihood that the outcome will be influenced by lack of blinding. The guidance suggests that a common assessment of risk be completed for all subjective outcomes (e.g. distress) as compared to objective outcomes (e.g. mortality) (Higgins 2011a). Accordingly, we will group all 'subjective' primary and secondary outcomes as being at high risk of bias if blinding is unsuccessful. However, the mortality outcome is unlikely to be influenced by lack of blinding. Therefore we will treat this as a 'low risk of bias' even if blinding is unsuccessful.

Measures of treatment effect

If appropriate, we will undertake meta‐analysis of the primary and secondary outcomes using RevMan (RevMan 2014). We will evaluate the direction and size of the effect as well as looking at the consistency of the effect across the selected studies. We will appraise the strength of the evidence using the grading system recommended by Cochrane (van Tulder 2003). To measure treatment effect, we will calculate a summary statistic for each study followed by an overall average treatment effect. We will use odds ratios (ORs) with 95% confidence intervals (CIs) for each study to determine whether pain was reduced or not.

We will treat our primary outcome as a binary outcome. This will aid interpretation of the findings for clinicians and address the heterogeneity of pain data. Pain outcome data in eligible studies is likely to be presented as binary or ordinal data. This will involve transforming data by aggregating adjacent categories. Decisions related to dichotomising data will be informed primarily by clinical considerations with reference to the study population. Even though ORs will be used to detect treatment effect, we will present findings as risk ratios (RRs) (or relative risk reduction) in order to aid the use and interpretation of the findings by end users.

We will use either a fixed‐effect or a random‐effects model for meta‐analysis. It is likely that we will use a random‐effects model as the true effect size may not be due to chance alone. Eligible studies will most probably have been conducted with different populations, countries and years, for example. It is therefore likely that we may incorporate the assumption of heterogeneity in our review. However, should we detect one true underlying fixed‐effect size, we will use a fixed‐effect model.

For secondary outcomes, we will either calculate standardised mean differences (SMDs) with 95% CIs in both intervention(s) and comparator(s) in order to show the intervention effect involving continuous data. For measures in the form of binary data, we will calculate ORs with 95% CIs. Ordinal data may be transformed into dichotomous data by aggregating adjacent categories together (informed by clinical judgement). If the same continuous outcome measure is used in all studies and measured in the same way, then we will average the results and we will calculate a mean difference (MD). If the outcome measures are the same, but they are measured differently in each study, we will calculate the SMD. A SMD of less than or equal to 0.2 will constitute a small effect, 0.2 to 0.5 will constitute a moderate effect and ≥ 0.8 will constitute a large effect. We will assume statistical significance using a P value of < 0.05.

Unit of analysis issues

We will address issues in the analysis of studies with particular characteristics, for example cross‐over trials and cluster randomised trials, once, and if, we identify such studies. We will report intra‐cluster correlations for cluster trials and we will complete adjustments where necessary. We intend to use the intra‐class correlation coefficient (ICC) supplied in eligible studies to adjust for meta‐analysis. If this value is not supplied in the article, we will seek this information from the study authors. If still unavailable, we will estimate an intra‐class correlation to allow for meta‐analysis.

Dealing with missing data

When data are missing from a study, we will contact the original investigator for clarification and additional information where possible. We will describe any strategy used for imputing missing data, as well as justifying the choice of the strategy used. We are also expecting to find studies with missing intervention data (number of staff involved, skills and so on). We will examine the potential impact of these missing data on the findings of the review in the 'Discussion' section of the review. We will seek clarity from study authors regarding study population and interventions where required, especially to aid examination of the components of the intervention.

Assessment of heterogeneity

We will examine and assess heterogeneity through the following three measures:

• inspecting the studies to examine for plausible areas of heterogeneity based on clinical factors that may influence findings of our meta‐analysis;

• inspecting the forest plots;

• using the I² statistics to examine the extent and impact of heterogeneity between included studies.

We will explore reasons for heterogeneity in sensitivity analysis should high heterogeneity be identified (I² statistic ≥ 75%) (Higgins 2011a).

Assessment of reporting biases

In order to detect and manage reporting bias, we will take steps to attend to:

• multiple (publication) bias by contacting study authors to ascertain whether duplication has occurred;

• location bias by searching relevant national and international trial registries for all relevant studies included (e.g. CENTRAL);

• language bias by including studies published in languages other than English, where possible, and if their inclusion is not feasible then we will report on these studies to identify that their data was not included in the review; and

• outcomes reporting (including non‐publication of economic evaluation outlined in the protocol) through comparing the findings in eligible studies with published protocols where available. Where published protocols are unavailable, we will ask study authors to supply them.

In addition, if there are more than 10 included studies in our meta‐analysis, we will use funnel plots and visually inspect them for asymmetry/symmetry as a means of determining the effects of any eligible small study. We will also conduct relevant tests for asymmetry influenced by data type (e.g. continuous or dichotomous), to assist with examining publication bias and to overcome any reliance on visual inspection (Lau 2006). Should we identify small‐study effects, we will conduct sensitivity analysis to examine different assumptions and their impact on the review findings. We will determine fixed‐effect and random‐effects estimates of the intervention effect if it becomes evident that there is between‐study heterogeneity. When we observe asymmetry, we will consider publication bias as one (of several) plausible explanations (Sterne 2001).

As the potential for bias is greater in a non‐randomised study than in a well‐conducted randomised trial (Kato 1999), we will pay particular attention to selection bias and reporting bias for non‐randomised studies. We will critically appraise all studies and assess their risk of bias following guidance from the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). Non‐randomised studies are generally assessed as low in quality, but can be appraised as higher if indicated by a large magnitude of effect or lack of concern about confounding (Higginson 2008). We expect pooling of effect estimates from non‐randomised studies to be the exception rather than the rule, and will follow Cochrane Handbook for Systematic Reviews of Interventions guidance at all times (Higgins 2011a).

Data synthesis

Should the eligible studies not be sufficiently homogenous to permit meta‐analysis, we will extract quantitative data (means, standard deviations, frequencies and proportions, test coefficients, 95% CIs and effects sizes, where available) and we will employ techniques used in narrative synthesis to analyse the data, including:

• tabulation, which will involve inserting the main elements of extracted data into a table format;

• textual descriptions, which will involve collating a summary description of each included study;

• clustering of group textual descriptions according to attributes; and

• vote counting to determine how often certain attributes were reported (Rodgers 2009).

Where possible, we will include qualitative data from nested or embedded qualitative studies where qualitative data has been used as part of the trial to assess the effectiveness or cost‐effectiveness of the intervention. We will analyse these through narrative synthesis methods.

Subgroup analysis and investigation of heterogeneity

As part of our primary objective, we will identify the effective components and determine the comparative effectiveness of inpatient specialist palliative care in acute hospitals for adults with advanced illness and their caregivers. We will compare the resources and costs associated with these services and determine their cost‐effectiveness; compare the effectiveness by disease type (e.g. malignant and non‐malignant groups), inpatient settings and country; examine other sources of heterogeneity, including interventions offering only single or few components of palliative care, and the applicability of meta‐analysis.

We will perform subgroup analysis using the following components known to influence the effectiveness of inpatient specialist care and in relation to particular patient groups.

• Patient characteristic of disease type, including malignant and non‐malignant disease to improve the evidence base for different types of palliative care populations (Higginson 2010). Those with malignant disease will be those diagnosed with malignant neoplasms (ICD‐10 codes: C00‐C97). Those with non‐malignant and other health‐related conditions, will include those diagnosed with: heart disease, including cerebrovascular disease (ICD‐10 codes: I00‐I52, I60‐69), renal disease (ICD‐10 codes: N17, N18, N28, I12, I13), liver disease (ICD‐10 codes: K70‐K77), respiratory disease (ICD‐10 codes: J06‐J18, J20‐22, J40‐47, J96), neurodegenerative disease (Huntington’s disease (ICD‐10 code: G10), Parkinson’s disease (ICD‐10 code: G20), multiple sclerosis (ICD‐10 code: G35), motor neuron disease (ICD‐10 code: G12.2)), multi‐system degeneration (ICD‐10 code: G90.3), progressive supranuclear ophthalmoplegia (ICD‐10 code: G23.1), Alzheimer’s dementia and senility (ICD‐10 codes: F01, F03, G20, R54), and HIV/AIDS (ICD‐10 codes: B20‐B24);

• frailty associated with advanced age due to how valuable these findings will be to society and future commissioning of services;

• inpatient specialist palliative care team composition (e.g. physician‐led as compared to nurse‐led palliative care services) and organisation (e.g. 24‐hour access versus temporally restricted access) to examine the effectiveness of different models of service provision and to inform service delivery and configuration. This subgroup analysis will aid the identification of key components of inpatient specialist palliative care models (Higginson 2010). In addition we will consider which models of specialist palliative care work best for which patients. During this review, we will measure what the study authors mean by specialist in patient palliative care in each instance. We will aim to develop a taxonomy of the components. As such we will aim to fully understand what the intervention is and clearly present this, allowing clear and transparent conclusions about the data to be reached. In addition, this will provide an important methodological contribution to palliative care for future studies. The review will also generate insights into barriers and facilitators and the different points in the pathway in which specialist palliative care could have an impact;

• we will also explore the country of origin due to differences in care structures and the availability of inpatient specialist palliative care, and any associated impact of this on effectiveness and cost‐effectiveness.

Sensitivity analysis

We plan to conduct sensitivity analyses of heterogeneity related to clinical (e.g. intervention type, patient population) and statistical reasons inherent within eligible studies. The I² statistic will help us examine the extent and impact of heterogeneity between included studies. We will explore reasons for heterogeneity using sensitivity analysis when high heterogeneity (I² statistic ≥ 75%) is evident (Higgins 2011a).