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Hospitalisation in short-stay units for internal medicine diseases and conditions (Protocol) Strøm C, Fabritius ML, Rasmussen LS, Schmidt TA, Jakobsen JC

Strøm C, Fabritius ML, Rasmussen LS, Schmidt TA, Jakobsen JC. Hospitalisation in short-stay units for internal medicine diseases and conditions. Cochrane Database of Systematic Reviews 2016, Issue 9. Art. No.: CD012370. DOI: 10.1002/14651858.CD012370.

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Hospitalisation in short-stay units for internal medicine diseases and conditions (Protocol) Copyright © 2016 The Cochrane Collaboration. Published by John Wiley & Sons, Ltd.

TABLE OF CONTENTS HEADER . . . . . . . . . . ABSTRACT . . . . . . . . . BACKGROUND . . . . . . . OBJECTIVES . . . . . . . . METHODS . . . . . . . . . ACKNOWLEDGEMENTS . . . REFERENCES . . . . . . . . APPENDICES . . . . . . . . CONTRIBUTIONS OF AUTHORS DECLARATIONS OF INTEREST . SOURCES OF SUPPORT . . . . NOTES . . . . . . . . . . .

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[Intervention Protocol]

Hospitalisation in short-stay units for internal medicine diseases and conditions Camilla Strøm1 , Maria Louise Fabritius2 , Lars S Rasmussen2 , Thomas A Schmidt1 , Janus C Jakobsen3,4 1 Department of Emergency Medicine, Holbaek Hospital, University of Copenhagen, Holbaek, Denmark. 2 Department of Anaesthesia,

Centre of Head and Orthopaedics, Rigshospitalet, University of Copenhagen, Copenhagen, Denmark. 3 The Cochrane Hepato-Biliary Group, Copenhagen Trial Unit, Centre for Clinical Intervention Research, Department 7812, Rigshospitalet, Copenhagen University Hospital, Copenhagen, Denmark. 4 Department of Cardiology, Holbaek Hospital, Holbaek, Denmark Contact address: Camilla Strøm, Department of Emergency Medicine, Holbaek Hospital, University of Copenhagen, Holbaek, 4300, Denmark. [email protected]. [email protected]. Editorial group: Cochrane Effective Practice and Organisation of Care Group. Publication status and date: New, published in Issue 9, 2016. Citation: Strøm C, Fabritius ML, Rasmussen LS, Schmidt TA, Jakobsen JC. Hospitalisation in short-stay units for internal medicine diseases and conditions. Cochrane Database of Systematic Reviews 2016, Issue 9. Art. No.: CD012370. DOI: 10.1002/14651858.CD012370. Copyright © 2016 The Cochrane Collaboration. Published by John Wiley & Sons, Ltd.

ABSTRACT This is the protocol for a review and there is no abstract. The objectives are as follows: To assess the beneficial and harmful effects of hospitalisation in a short-stay unit versus usual care for patients with internal medicine diseases and conditions.

BACKGROUND

Description of the condition Patients with internal medicine diseases account for the majority of health care provided in hospitals. Worldwide, internal medicine diseases such as diabetes and cardiovascular disease are the leading cause of disability and death (CDC 2013; EFIM 2007; WHO 2011). Prevalences of chronic internal medicine diseases are rapidly rising; currently, one in two adults is affected by at least one chronic disease (Gerteis 2014; Pfuntner 2013; WHO 2011; Wolff 2002). This spreads into the acute care system as an increasing amount of patients needs acute hospitalisation due to worsening of symptoms of a chronic disease (Dang-Tan 2015; WHO 2011). Additionally, common infectious internal medicine diseases such as pneumo-

nia or urinary tract infections are still the main reason for acute hospitalisation (Christensen 2009; Pfuntner 2013; Weiss 2014). Infectious diseases continue to be associated with substantial morbidity and mortality (Christensen 2009; Lowthian 2011). Despite theoretical advances in sanitation and health care, the annual hospitalisation rate for infectious diseases has increased over recent decades; the incidence has been estimated at 15 hospitalisations per 1000 persons per year in the USA (Christensen 2009). In this review, we study hospitalised patients with internal medicine diseases and conditions. We use the term ’internal medicine diseases and conditions’ to cover all internal medicine diagnoses and conditions that usually are treated at internal medicine departments. Management of these patients can be challenging; they can present with several non-specific symptoms from various organ systems and different diseases, both acute and chronic, and require complex investigations and multifaceted care such as


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the involvement of different internal medicine specialists, special nursing expertise, respiratory therapy, and physiotherapy.

Description of the intervention The intervention of interest is short-stay unit hospitalisation for internal medicine patients. Since the 1960s, short-stay units have been introduced increasingly in Western countries (Cerce 1981; Galipeau 2015). The earliest models targeted paediatric and surgical patients (Laskin 1972). Subsequent models have targeted internal medicine patients and mentally-ill patients (Daly 2003). There is no widely-accepted definition of short-stay units, but usually a short-stay unit is an in-hospital ward that provides shortterm hospitalisation or observation for selected patient groups. Usually the maximum length of stay is up to 48 or 72 hours. Shortstay units have various names, e.g. short observation unit, medical assessment and planning unit, quick diagnostic unit. Shortstay units may differ from each other in characteristics and features, and they may provide different types of care for patients. Many use strict admission and discharge criteria (Galipeau 2015; Gaspoz 1991). Specialised short-stay units only admit certain patient groups such as patients with chest pain or asthma (Broquetas 2008; Jibrin 2008), while multipurpose short-stay units admit patients with a wide range of clinical symptoms and conditions. Some short-stay units function as separate entities while others function as part of a larger department, often as part of an emergency department (Daly 2003; Damiani 2011; Galipeau 2015). A short-stay unit can therefore be run either by dedicated house staff or hospitalists, or under the clinical governance of the emergency department staff. Short-stay units are usually equipped with emergency medical treatment facilities, and sometimes advanced diagnostic equipment such as radiologic or laboratory facilities (Daly 2003; Miller 2010; Miller 2013). Often, patients admitted to a short-stay unit have received an evaluation upon arrival in an emergency department (physical exam, medical history, medications review) and an initial plan for treatment of acute symptoms (Juan 2006). In the short-stay unit, further observation, diagnostics and treatments are carried out (Downing 2008). Compared to care in an ordinary ward, many short-stay units apply components that potentially streamline patient care, and accelerate the diagnostic process or time of rehabilitation. These components may include the provision of immediate access to diagnostic facilities, the use of standardised treatment protocols, or the application of strict admission criteria (Daly 2003; Galipeau 2015; Gaspoz 1991). To optimise treatment and early discharge, evaluation upon arrival in a short-stay unit often includes assessments of functional capacity and the need for support after discharge, and planning of out-of-hospital care for non-acute medical problems (Daly 2003; Galipeau 2015). The number of acute hospital admissions is expected to rise in response to ageing populations, growing numbers of patients with chronic diseases, and increasing demands for improved quality

of care (Cowling 2014). Therefore, both financial and organisational resources are and will be increasingly challenged (McKee 2003). Hospitals are trying to adapt to these challenges in various ways; one is to facilitate shorter and more effective hospital stays (Downing 2008). Short-stay units are thought to provide this kind of accelerated care, sometimes referred to as fast-track care. Additionally, short-stay units may alleviate emergency overcrowding, where the demand for emergency services exceeds the ability to provide care for patients in a reasonable amount of time. In a recent report by the American College of Emergency Physicians, establishment of short-stay units in hospitals was described as an important step to alleviate overcrowding in emergency departments (ACEP 2008). Reducing the time of bed occupancy and rates of overcrowding by short-stay unit hospitalisation may be an indicator of good performance at an organisational level, but the advantages or disadvantages for patients treated in such systems are unclear (Galipeau 2015).

How the intervention might work Short-stay units are likely to work as an intervention because they may: 1) result in less exposure to adverse events during hospitalisation; 2) reflect a more efficient service design; and 3) provide tailored care for selected patients. The hospital environment is associated with numerous hazards. Adverse events during hospitalisation occur frequently (Brennan 1991); e.g. cognitive disturbances such as delirium in older patients (Inouye 1990), or nosocomial infections (Baker 2004; Brennan 1991; Thomas 2000). Despite high hospital sanitation standards, hospitalised patients cannot be entirely isolated from harmful microbes; infections may spread to susceptible patients from other patients, healthcare staff, contaminated equipment, or air droplets. Large population studies have estimated that 3% to 17% of all hospitalised patients experience an adverse event during an episode of hospitalisation, and adverse events are associated with substantial physical impairment and mortality (Baker 2004; Brennan 1991; Thomas 2000; Vries 2008). Moreover, adverse events are associated with prolonged in-hospital length of stay (Classen 1997), but it is unclear to what extent adverse events lead to prolonged length of stay, or whether prolonged hospital stay increases the risk of an adverse event. We hypothesise that minimising length of stay by short-stay unit hospitalisation results in less exposure to adverse events during hospitalisation. Reducing or minimising the time spent in hospital is an implicit aim of short-stay unit hospitalisation. Optimising the diagnostic, treatment and rehabilitation processes in a short-stay unit may translate into a more efficient service design, which could improve patient outcomes. Tailored care with focused assessments or specific treatment protocols may enhance recovery for some patients. Many short-stay units incorporate components of accelerated care into patient care, in a manner similar to those studied in surgical populations, sometimes referred to as the ’enhanced recovery after


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surgery’ programme (ERAS). ERAS is based on the application of standardised treatment protocols and certain fast-track elements such as accelerated mobilisation, early removal of drains or tubes, and early discharge planning. Systematic reviews have shown that ERAS seems to reduce morbidity rates, speed up recovery, and shorten the duration of hospital stay (Spanjersberg 2011; Wind 2006). However, the relative contribution of each of the ERAS programme components remains uncertain. We find it possible that patients with internal medicine diseases and conditions may benefit in a similar way from streamlined care in short-stay units. Mobilisation and prevention of prolonged bed rest may improve rehabilitation and prevent functional decline related to hospitalisation. Early discharge planning may facilitate faster and appropriate discharge processes (Daly 2003; Galipeau 2015).

Why it is important to do this review The treatment of patients with internal medicine diseases accounts for the vast majority of healthcare expenditure (WHO 2011) and costs are expected to rise significantly (Cowling 2014) - especially because the global population is dramatically ageing (UN 2013). There is an urgent need to explore how healthcare systems successfully can adapt to this challenge, while providing the best possible care for this patient group. Implementation of short-stay units may be one useful strategy to cope with the increasing demand for hospital care. Already, there has been a substantial growth in shortstay units (Salazar 2007). Patients, payers, and healthcare systems have great interest in knowing the relative benefits and harms of short-stay unit hospitalisation for patients with internal medicine diseases and conditions, but the evidence in this particular area is sparse. In a review more than a decade old, Daly et al. concluded that short-stay units had the potential to reduce patients’ length of stay, improve the efficiency of emergency departments, and improve cost effectiveness (Daly 2003). Since then, the authors of two systematic reviews have proposed that treatment of internal medicine diseases and conditions in short-stay units may reduce inpatient mortality and length of stay without increasing readmission rates (Damiani 2011; Scott 2009). Authors of a recent systematic review described the effect of multipurpose short-stay units on emergency department overcrowding, assessing the units’ effectiveness and safety as reported in trials conducted in countries with healthcare systems similar to Canada (Galipeau 2015). They found the evidence to be insufficient (Galipeau 2015). We will investigate whether short-stay unit hospitalisation is a viable alternative to usual care for patients with internal medicine diseases and conditions. This review will add to the current body of evidence by assessing beneficial and harmful effects of both specialised and multipurpose short-stay units, taking into account the risk of systematic error.

OBJECTIVES To assess the beneficial and harmful effects of hospitalisation in a short-stay unit versus usual care for patients with internal medicine diseases and conditions.

METHODS

Criteria for considering studies for this review

Types of studies We will include randomised clinical trials (RCTs) including cluster randomised trials and randomised stepped-wedge design trials. A preliminary literature search revealed several randomised trials. To ensure scientific rigour when assessing intervention effects, we have chosen only to include trials with a randomised design. Observational studies cannot reliably evaluate intervention effects (Hemkens 2016), and non-randomised trials are prone to selection bias and confounding (Chapter 13, Higgins 2011). Trials will be included irrespective of publication date, publication type and status, reported outcomes, and language. Types of participants We will include trials randomising hospitalised adult participants (age 18 years or above) receiving care for any internal medicine disease or condition (such as pneumonia, chronic obstructive pulmonary disease, chest pain or dyspnoea). Trials that specifically randomise surgical, obstetric or gynaecological patients, patients with mental illnesses or ambulatory patients will not be included. Should a trial include mixed populations (e.g. both internal medicine patients and surgical patients), we will include the trial, but only evaluate outcomes for the hospitalised internal medicine patients, if data are available. Types of interventions

Experimental group

Hospitalised treatment in a short-stay unit. As indicated in the ’Description of the intervention’ section, there is no widely-accepted definition of short-stay units. We define a short-stay unit as a hospital ward where the targeted length of stay for patients is less than or equal to 5 days. However, to avoid the exclusion of potentially-relevant trials, we will accept the intervention if the trialists classify the experimental intervention as, or use the term, ’short-stay unit’, ‘emergency department observation unit’, ‘fast track medical ward’, or similar terms. By handsearching the literature, we have identified a list of different names of short-stay


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units (Appendix 1). We will accept all of these terms, but the list is not expected to be comprehensive and other relevant terms will be accepted. We will both include multipurpose and specialised short-stay units. The details of each unit will be reported, because there will be variation from trial to trial. In a subgroup analysis, we will investigate whether there are differences in outcomes between trials that fulfil our proposed short-stay unit definition compared to the other trials (see Subgroup analysis and investigation of heterogeneity).

6. Total length of stay in hospital. As short stay hospitalisation is an implicit aim of the intervention, we will evaluate this outcome with caution. We will report comparable cost narratively if reported in the included trials. We will estimate all outcomes at two time points: • the time point closest to 90 days after randomisation (this will be the outcome of primary interest); and • at maximum follow-up.

Control group

Reporting of the outcomes listed above will not be an inclusion criterion for the review; we will include trials regardless of the assessed outcomes. All outcomes will be included in a ’Summary of findings’ table.

Usual care/hospitalisation (as defined by trialists).

Types of outcome measures We will assess the following outcomes (in accordance with their classification in EPOC 2013a): • patient-centred outcomes: all-cause mortality, activities of daily living, quality of life. • adverse events or harms: serious adverse events, non-serious adverse events. • utilisation, coverage, or access: hospital readmission, length of stay in hospital, transfer to another department.

Primary outcomes

1. All-cause mortality. 2. Proportion of participants with one or more serious adverse event as defined by the International Committee of Harmonisation-Good Clinical Practice (ICH-GCP): “any untoward medical occurrence that resulted in death, was life threatening, required inpatient hospitalisation or prolongation of existing hospitalisation, resulted in persistent or significant disability/incapacity” (ICH-GCP 1997).

Secondary outcomes

1. Quality of life measured on any valid scale, such as the 36item Short Form Health Survey (SF-36) (Ware 1992). 2. Activities of daily living measured by any scale, such as Lawton’s Instrumental Activities of Daily Living score (iADL) (Lawton 1969). 3. Proportion of patients that are readmitted after index hospitalisation. 4. Non-serious adverse events (registration of any untoward medical occurrence in a patient, which does not necessarily have a causal relationship with a given intervention). 5. Transfer to another department (number of patients that have been transferred to hospitalisation in another department after initial admission to either a short-stay unit or unit in control group).

Search methods for identification of studies

Electronic searches The EPOC Information Specialist (IS) will develop the search strategies in consultation with the authors. We will search the Cochrane Database of Systematic Reviews (CDSR) and the Database of Abstracts of Reviews of Effects (DARE) for primary trials included in related systematic reviews. We will search the following databases (from inception): • Cochrane Central Register of Controlled Trials (CENTRAL), including the EPOC Group Specialised Register; • MEDLINE, 1946 to present, In-Process and other nonindexed citations, OvidSP; • Embase, 1974 to present, OvidSP. The search strategies will be comprised of keywords and controlled vocabulary terms. Language limits will not be applied. All databases will be searched from inception to the date of search. We will use a methodology search filter to limit retrieval to appropriate trial designs; namely, a modified version of the Cochrane Highly Sensitive Search Strategy (sensitivity and precision maximizing version - 2008 revision) (Lefebvre 2011) to identify randomised trials (Higgins 2011). See Appendix 2 for the MEDLINE search strategy, which will be adapted for other databases. Searching other resources We will conduct a grey literature search and search other sources listed below to identify trials not indexed in the databases listed above. We will search: • International Clinical Trials Registry Platform (ICTRP), World Health Organization (WHO); • ClinicalTrials.gov, US National Institutes of Health (NIH) (clinicaltrials.gov); • OpenGrey;


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• Grey Literature Report (New York Academy of Medicine) ( www.greylit.org); • Health Services Research Projects in Progress (HSRProj) (NICHSR 2014). We will also: • contact researchers with expertise relevant to the review topic; • search other web sources such as the King’s Fund library database (www.kingsfund.org.uk/library); • if required, contact authors of relevant trials/reviews to clarify reported information or seek unpublished results/data; • search individual journals and conference proceedings; • conduct a forward citation search of included trials using Science Citation Index via ISI Web of Science ( pcs.webofknowledge.com); In appendices, we will provide the search strategies used, including a list of sources screened and relevant reviews/primary trials reviewed.

Data collection and analysis We will perform the review according to the recommendations of the Cochrane Collaboration (Higgins 2011) and the Effective Practice and Organisation of Care Group (EPOC 2013b).

Selection of studies We will download all titles and abstracts retrieved by the electronic search to the web-based software platform, Covidence (Covidence 2015) and remove duplicates. Two review authors (CS and MF) will independently assess all of the titles and abstracts for eligibility. We will exclude trials that obviously do not match the inclusion criteria (see trial screening template - Appendix 3). Two review authors will independently assess the full-text reports of potentially eligible trials. Those that clearly do not meet the eligibility criteria will be excluded without reasons being reported in the review. We will resolve any disagreements on trial eligibility by discussion and consensus. If no agreement can be reached, we will confer with a third review author (JCJ). If discrepancies between authors are not easily resolved, the contact editor will be consulted. We will list trials that were thought likely to be relevant but that were subsequently excluded, in a ’Characteristics of excluded studies’ table and provide reasons for their exclusion (EPOC 2013c). In the case of ongoing trials, we will contact the trial’s coordinator to collect information on the characteristics of the trial. If the trial fulfils the inclusion criteria in Appendix 3, we will, if possible, report preliminary results. We will collate multiple reports of the same trial so that each trial rather than each report is the unit of interest in the review.

We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009).

Data extraction and management We will use a modified EPOC data collection form (EPOC Supplementary materials), which has been piloted on at least one included trial in the review, to capture trial characteristics and outcome data. Two review authors (CS and MF) will independently extract the following characteristics from included trials: 1. Name and definition of short-stay unit, including defined maximum stay in short-stay unit (e.g. 72 hours); 2. Name and definition of control arm (usual care/ hospitalisation); 3. Methods: trial design, number of trial centres and location, trial setting, withdrawals, dates of trial, sample size calculation; 4. Participants: number, median age, age range, sex, condition, severity of condition, diagnostic criteria, inclusion criteria, exclusion criteria, other relevant characteristics; 5. Interventions: intervention components, treatment protocols, early mobilisation, early discharge planning, fidelity assessment, type of staffing, creation of new team of healthcare providers, staffing per patient bed (e.g. physicians, nurses), clinical specialty of providers of care, other interventions not described elsewhere; 6. Treatment in control group: treatment protocols, early mobilisation, early discharge planning, fidelity assessment, type of staffing, creation of new team of healthcare providers, staffing per patient bed (e.g. physicians, nurses), clinical specialty of providers of care, other interventions not described elsewhere; 7. Outcomes: primary and other outcomes specified and collected, time points reported (see Types of outcome measures); 8. ’Risk of bias’ assessment (see Assessment of risk of bias in included studies); 9. Notes: funding for trial, notable conflicts of interest of trial authors, ethical approval. We will note in a ’Characteristics of included studies’ table if outcome data was reported in an unusable way. We will resolve disagreements by consensus or by involving a third review author (JCJ).

Assessment of risk of bias in included studies Two review authors (CS and MF) will independently evaluate the risk of bias for each trial using the criteria outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and the guidance from the EPOC Group (EPOC 2015a). Any disagreements will be resolved by discussion or by involving a third review author (JCJ). We will assess all trials for allocation sequence generation, allocation concealment, baseline outcome measurement, baseline characteristics, blinding of outcome assessment, incomplete outcome


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data, contamination, selective outcome reporting, and other risk of bias. We consider it impossible for any trials to have blinded participants or treatment providers; therefore, we have chosen not to include blinding of participants or treatment providers as bias domains. We will assess each potential source of bias as high, low or unclear and provide a quote from the trial report together with a justification for our judgment in the ’Risk of bias’ table. We will summarise the ’Risk of bias’ judgements across different trials for each of the domains listed below. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the ’Risk of bias’ table. We will present our judgments in a ‘Risk of bias graph’ and ’Risk of bias summary’ figure. When considering intervention effects, we will take into account the risk of bias for the trials that contribute to that outcome.

Risk of bias criteria

Allocation sequence generation Low risk of bias: if a random component in the sequence generation process is described (e.g. random number generation, toss of coin, throwing dice). Unclear: if the method of randomisation is not described explicitly. High risk of bias: if a non-random method is used (e.g. performed by date of admission).

Allocation concealment Low risk of bias: if the unit of allocation was by institution and allocation was performed on all units at the start of the trial; or if the unit of allocation was by patient and there was some form of centralised randomisation scheme: an on-site computer system or sealed opaque envelopes were used; or if other descriptions of convincing concealment of allocation are provided. Unclear: if no information on allocation concealment is specified. High risk of bias: allocation method allowed the investigators or participants to know the next allocation, e.g. open allocation sequence list, unsealed envelopes.

(e.g. baseline adjustment analysis or intention-to-treat analysis) the domain will be re-scored as “Low risk”.

Baseline characteristics Low risk of bias: if baseline characteristics of the intervention and control providers are reported and similar. Unclear: if no information on baseline characteristics is specified. High risk of bias: if there is no report of characteristics in text or tables or if there are differences between control and intervention providers.

Blinding of outcome assessment Low risk of bias: if the authors state explicitly that the primary outcome variables were assessed and analysed blindly, or the outcomes are objective, e.g. mortality. Unclear: if no information on blinding is specified. High risk of bias: if the outcomes were not assessed blindly. We will consider blinding separately for different key outcomes where necessary (e.g. the risk of bias for all-cause mortality may be very different than for patient-reported activities of daily living score).

Incomplete outcome data Low risk of bias: if clearly stated that there were no withdrawals or dropouts; or if the numbers of and reasons for all dropouts and withdrawals are clearly stated and can be described as similar in both groups and the trial handles missing data appropriately in an intention-to-treat analysis using proper methodology e.g. multiple imputations. Unclear: if the numbers of or reasons for withdrawals and dropouts are not clearly described. High risk of bias: if the pattern of withdrawals and dropouts can be described as being different in the groups, or the trial uses improper methodology in dealing with missing data e.g. last observation carried forward. If the number of withdrawals and dropouts are over 15%, the trial will be judged as at high risk of bias due to incomplete outcome data.

Baseline outcome measurement Low risk of bias: if relevant performance or patient outcomes were measured prior to the intervention, and no important differences were present across trial groups, or if imbalanced, appropriate adjusted analysis was performed (e.g. analysis of covariance). Unclear: if no information on baseline measurement is specified. High risk of bias: if important differences were present and not adjusted for in analysis. If a trial is deemed at “Unclear risk” or “High risk” for this domain, but there are sufficient data in the paper to do an adjusted analysis

Contamination Low risk of bias: if it is unlikely that the control participants were admitted to a short-stay unit (experimental intervention) (or vice versa) during the intervention period. Unclear: if no information on risk of contamination is specified. High risk of bias: if it is likely that the control participants were admitted to a short-stay unit (experimental intervention) (or vice versa) during the intervention period.


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Selective outcome reporting Low risk of bias: if a trial protocol is published in a journal or a trial registry before or at the time the trial is begun and the outcomes called for in the protocol are reported on, or if there is no evidence that outcomes are selectively reported (e.g. all relevant outcomes in the methods section are reported in the results section). Unclear: if not specified. High risk of bias: if the outcomes that were called for in a protocol, in a trial registry or in the methods section, are not reported on.

Other risk of bias Low risk of bias: if the trial appears to be free of other components (e.g. industry bias, academic bias) that could put it at risk of bias. Unclear: the trial may or may not be free of other components that put it at risk of bias. High risk of bias: if there are other factors in the trial that could put it at risk of bias (for example, authors have conducted trials on the same topic).

Overall risk of bias We will evaluate the risk of bias for the trial in general, and the risk of bias for each outcome for the following bias domains: blinding of outcome assessors, incomplete outcome data, and selective outcome reporting. Low risk of bias: if all of the bias domains in the above paragraphs are classified as ‘low risk of bias’. High risk of bias: if one or more of the above bias domains have been classified as ‘unclear’ or ‘high risk of bias’

Assesment of bias in conducting the systematic review We will conduct the review according to this published protocol and report any deviations from it in the ’Differences between protocol and review’ section of the systematic review.

with great caution due to a number of methodological limitations (Higgins 2011). We will report treatment effects using both numbers and qualitative statements. We will not report results as being statistically significant or non-significant (EPOC 2013f). We will discuss the precision of the outcome estimates, and we will consider whether the size of the effect is important, less important or not important according to the EPOC guidance (EPOC 2013b). For each outcome, we have predefined a minimal relevant clinical difference between the two interventions. We will use the following minimal relevant clinical differences: • All-cause mortality: relative risk reduction or increase of 15%. • Serious adverse event: relative risk reduction or increase of 20% (Baker 2004; Brennan 1991). • Quality of life: We will use the observed standard deviation (SD), a clinically-relevant mean difference equal to SD/2 (Jakobsen 2014). • Activities of daily living: We will use the observed SD, a clinically-relevant mean difference equal to SD/2 (Jakobsen 2014). • Readmission: relative risk reduction or increase of 20% (Miller 2013; Robert 1997). • Non-serious adverse events: relative risk reduction or increase of 20%. • Transfer to other department: relative risk reduction or increase of 30%. • Total length of stay in hospital: relative risk reduction or increase of 20% (Miller 2010; Miller 2013; Robert 1997).

Unit of analysis issues We will assess the effects of randomised clinical trials and cluster randomised trials separately. We will use the generic inverse variance method according to chapter 9 of the Cochrane Handbook (Higgins 2011) to meta-analyse both types of trials in one analysis. If the trialists have not used appropriate methods to account for clustered data, then we will follow the instructions in the Cochrane Handbook chapter 16 to estimate ‘effective sample sizes’ (Higgins 2011).

Measures of treatment effect We will report the effects of the interventions using risk ratio and risk difference for dichotomous outcomes, together with the associated 95% confidence intervals (CIs). For continuous outcomes, both end scores and change scores will be included. We will present continuous outcomes by the mean difference (MD) with 95% CIs if all the trials use the same outcome scale. We will use the standardised mean difference (SMD) with 95% CIs when the trials measure the same continuous outcome, but use different scales. We will ensure that an increase in scores for continuous outcomes can be interpreted in the same way for each outcome, explain the direction to the reader and report where the directions were reversed, if this is necessary. We will interpret results of SMDs

Dealing with missing data We will contact investigators in order to obtain missing outcome data where possible (e.g. when a trial is identified as abstract only). We will state whether an intention-to-treat analysis has been performed. If proper methodology has been used in a trial to deal with missing data (e.g. multiple imputations), we will use these data in our analysis. We will not impute missing values for any outcomes. Sensitivity analyses will be conducted, including evaluation of best and worst case scenarios (see Sensitivity analysis). Finally, we will address the potential impact of missing data on the findings in the ’Discussion’ section of the review.


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Assessment of heterogeneity We will visually inspect forest plots to assess statistical heterogeneity. Statistical heterogeneity will be tested using the Chi² test with a significance level set at P ≤ 0.10, and will be measured by I² statistics for quantification of inconsistencies and by D² statistics for information size adjustments (Wetterslev 2009). Unless unexpected clinical or statistical heterogeneity is observed, we will conduct a meta-analysis if there are data on separate outcomes from two or more trials (Jakobsen 2014). If we identify substantial heterogeneity, we will explore it by prespecified subgroup analysis and inspection of trial characteristics. Assessment of reporting biases We will attempt to contact trial authors asking them to provide missing outcome data. Where this is not possible, and the missing data are thought to introduce serious bias, the impact of including such trial in the overall assessment of results will be explored by a sensitivity analysis (see Sensitivity analysis). If we are able to pool more than ten trials, we will create and examine a funnel plot to explore possible publication biases, interpreting the results with caution (Sterne 2011). We will visually inspect funnel plots to assess the risk of bias. For dichotomous outcomes we will test asymmetry with the Harbord test (Harbord 2006). For continuous outcomes we will use the regression asymmetry test (Egger 1997) and the adjusted rank correlation (Begg 1994). If there are less than ten trials available, then publication bias will be deemed non-assessable.

We will perform both randomeffects meta-analyses (DerSimonian 1986) and Mantel-Haenszel fixed-effect meta-analyses (Mantel 1959). We will use the more conservative point estimate of the two; that is the estimate closest to zero effect (Jakobsen 2014). Should estimates be equal, we will use the estimate with the widest CI. In addition, we will use an eight-step procedure to assess whether or not the thresholds for statistical and clinical significance are crossed (Jakobsen 2014).

’Summary of findings’ table and assessing the certainty of evidence

We will assess the certainty of the evidence of the main intervention comparison using the five GRADE considerations (trial limitations, consistency of effect, imprecision, indirectness and publication bias) for the most important outcomes (Guyatt 2008), and present it alongside the data on effectiveness for each outcome. Two review authors (CS and MF) will grade the evidence according to the methods and recommendations described in section 8.5 and Chapter 12 of the Cochrane Handbook (Higgins 2011) and the EPOC worksheets (EPOC 2013d), using GRADEpro software (GRADEpro GDT 2015). Any disagreements will be resolved by discussion or by involving a third review author (JCJ). Final decisions will based on consensus and agreement in the group of authors. We will justify all decisions to down- or upgrade the certainty of the evidence in relation to each outcome using footnotes, and make comments to aid readers’ understanding of the review where necessary. We will summarise the results in a ’Summary of findings’ table.

Data synthesis Our primary conclusion will be based on low risk of bias trials. Results of high risk of bias trials will be interpreted with caution (Jakobsen 2014). We present outcome estimates as described in ’Measures of treatment effect’. We will undertake meta-analyses only where this is meaningful, i.e. if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense, and when no substantial heterogeneity is observed. We will perform standard meta-analysis using the statistical software Review Manager 5 (RevMan 2014). When analysing continuous outcomes, we will accept both end scores and change scores. In the case that both scores are reported, we will use the end score. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. intervention A versus usual care and intervention B versus usual care) must be entered into the same meta-analysis, we will halve the control group to avoid double counting. We will consider whether there is any additional outcome information that was not able to be incorporated into meta-analyses, note this in the comments, and state if it supports or contradicts the information from the meta-analyses. If it is not possible to meta-analyse the data we will summarise the results in the text.

Subgroup analysis and investigation of heterogeneity We will perform subgroup analysis on the following outcomes: 1. Mortality 2. Serious adverse events 3. Readmissions Following the guidance from EPOC (EPOC 2013e), these outcomes will be assessed according to the following possible explanatory factors. For each explanatory factor we have included the hypothesized direction of effect: 1. Risk of bias: Trials with low and lower risks of bias versus trials with trials with high risk of bias. We expect to observe an increased effect in the subgroup ’High risk of bias’. 2. Type of short-stay unit: Multipurpose short-stay units versus specialised short-stay units (e.g. chest pain short-stay unit, asthma short-stay unit). We expect to observe an increased effect in the subgroup ’Specialised short-stay units’. 3. Relation to emergency department: Emergency department based short-stay units versus non-emergency department based short-stay units. We expect to observe an increased effect in the subgroup ’Emergency department based short-stay unit.


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4. Type of intervention: Protocol specific intervention in short-stay unit versus not-protocol specific intervention in shortstay unit. We expect to observe an increased effect in the subgroup ’Protocol specific intervention’. 5. Age: Younger versus older patients (participants are defined as ‘older’ either by trialists or age above 65 years). We expect to observe an increased effect in the subgroup ’Younger patients’. 6. Time definition of unit: Trials declaring targeted length of stay of 5 or fewer days versus no defined or longer length of stay for patients. We expect to observe an increased effect in the subgroup ’Targeted length of stay of 5 or fewer days’. We will interpret the subgroup analysis results cautiously. Findings are to be regarded as observational. We anticipate there will be a small number of trials, and findings may be spurious. The test for subgroup differences will be analysed using test of interaction (Higgins 2011; RevMan 2014). In the case that important questions arise in the review process that we have not foreseen, we will, if possible, perform relevant post hoc analysis and clearly state this in the final manuscript.

Sensitivity analysis We will perform sensitivity analysis defined a priori to assess the robustness of our conclusions and explore its impact on effect sizes. This will involve: 1. Restricting the analysis to published trials. 2. Restricting the analysis to trials with a low risk of bias, as specified in Assessment of risk of bias in included studies. 3. Restricting the analysis to trials that have evaluated outcomes at least one time within 6 months of inclusion. 4. Imputing missing data. We will analyse the impact of missing data by best-worst case scenario analysis. For

dichotomous outcomes: ◦ ’best-worst-case’ scenario: It will be assumed that all participants lost to follow up in the experimental group survived and had no serious adverse event. ◦ ’worst-best-case’ scenario: It will be assumed that all participants lost to follow-up in the experimental group did not survive or had a serious adverse event. When analysing the continuous outcomes, a ‘beneficial outcome’ will be the group mean plus two standard deviations and a ‘harmful outcome’ will be the group mean minus two standard deviations. Secondly, we will use one standard deviation in another analysis (Jakobsen 2014). Results from both scenarios will be presented in our publication. The sensitivity analyses will be reported in a summary table.

ACKNOWLEDGEMENTS We acknowledge the help and support of the Cochrane Effective Practice and Organisation of Care Group, especially Paul Miller (PM) for tailoring the search strategy, and Managing Editor Julia Worswick (JW).The authors would also like to thank the following editors and peer referees who provided comments to improve the protocol: Gillian Leng (GL), Nkengafac Villyen Motaze (NVM), Monica Taljaard (MT), and Saul Blecker (SB). National Institute for Health Research (NIHR), via Cochrane Infrastructure funding to the Effective Practice and Organisation of Care (EPOC) Group. The views and opinions expressed herein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, National Health Service (NHS) or the Department of Health.

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APPENDICES

Appendix 1. Names and synonyms for short-stay units 1. 2. 3. 4. 5. 6. 7. 8. 9. 10. 11. 12. 13. 14. 15. 16. 17. 18. 19. 20. 21. 22. 23. 24. 25. 26. 27. 28. 29. 30. 31. 32. 33. 34. 35. 36. 37. 38. 39. 40. 41. 42. 43. 44. 45. 46. 47.

Accident and Emergency Department Short-stay Unit Acute Admission and Diagnostic Unit Acute Admissions Unit Acute Assessment Unit Acute Care for Elders Unit Acute Diagnostic Unit Acute Elderly Unit Acute Geriatric Unit Acute Geriatrics-based Wards Acute Medical Receiving Unit Acute Medical Unit Acute Medicine Unit Chest Pain Center Chest Pain Observation Unit Clinical Decision Unit Elderly Short-stay Unit Emergency Assessment Unit Emergency Department Asthma and Observation Unit Emergency Department Observation Unit Emergency Diagnostic and Treatment Unit Emergency Medical Assessment/Admissions Unit Emergency Short-stay Unit Extended Evaluation Unit Fast Specialized Ambulatory Care of Medical Disease Fast Track Medical Ward Geriatric Assessment Unit Geriatric Evaluation and Management Unit Immediate Care Clinics Medical Acute Care Unit Medical Assessment and Planning Unit Medical Assessment Unit Medical Short-stay Unit Observation Unit Orthogeriatric Unit for Acute Patients Quick and Early Diagnosis Unit Quick and Early Diagnostic Outpatient Unit Quick diagnostic unit Rapid diagnosis unit Short-stay Clinic Short-stay Hospital Unit Short-stay Medical Unit Short-stay Older Persons Unit Short-stay Unit Short-stay Unit for Older Persons Short-stay Observation Unit Short-stay Respiratory Unit Week Hospital


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Appendix 2. MEDLINE search strategy MEDLINE (OvidSP)

No.

Search terms

1

((emergency or geriatric? or medical) adj3 (planning or evaluation or assessment or asthma or observation or diagnos* or admission? or treatment) adj3 (unit? or ward?)).ti,ab

2

((quick or early or rapid) adj3 diagnos* adj3 (unit? or ward?)).ti,ab

3

week hospital?.ti,ab.

4

short stay*.ti.

5

(acute adj3 hospital adj3 (unit? or ward?)).ti,ab.

6

(chest pain adj3 (center? or centre? or unit? or ward?)).ti,ab

7

(clinical decision adj (unit? or ward?)).ti,ab.

8

(extended evaluation adj (unit? or ward?)).ti,ab.

9

((short stay* or fast-track or fasttrack or brief stay or short term or fast speciali*) adj3 (clinic? or unit? or ward? or care or department? or hospital* or service? or facilit* or center? or centre?)).ti,ab

10

(immediate care adj (clinic? or unit? or ward? or centre? or center?)).ti,ab

11

(observation adj (unit? or ward?)).ti,ab.

12

(acute adj3 (admission? or diagnos* or assessment or care or elderly or geriatric? or orthogeriatric? or medical or medicine) adj3 (unit? or ward?)).ti,ab

13

(orthogeriatric adj (unit? or ward?)).ti,ab.

14

or/1-13

15

exp randomized controlled trial/

16

controlled clinical trial.pt.

17

randomi#ed.ti,ab.

18

placebo.ab.

19

randomly.ti,ab.

20

Clinical Trials as topic.sh.

21

trial.ti.


14

(Continued)

22

or/15-21

23

exp animals/ not humans/

24

22 not 23

25

14 and 24

Search peer reviewed according to the PRESS checklist (Peer Review of Electronic Search Strategies).

Appendix 3. Screening algorithm for titles and abstracts 1. Does the trial compare treatment in a short-stay unit versus usual care? 2. Does the trial include adult patients (≥ 18years) 3. Does the trial include patients admitted to treatment for an internal medical disease or condition? 4. Does the trial meet design criteria; either 1) randomised controlled trial, 2) randomised step wedge design trial, 3) cluster randomised trial? If the answer to all the questions is “yes” or is ambiguous/”not clear”, the entire text of the paper will be examined.

CONTRIBUTIONS OF AUTHORS Conceiving the protocol: CS, JCJ Designing the protocol: CS, MF, LS, TAS, JCJ Coordinating the protocol: CS Designing search strategies: CS, PM Writing the protocol: CS Providing general advice on the protocol: CS, MF, JCJ, LS, TAS Securing funding for the protocol: CS, TAS Performing previous work that was the foundation of the current review: CS, LS, TAS

DECLARATIONS OF INTEREST Camilla Strøm has no conflicts of interest. Maria Louise Fabritius has no conflicts of interest. Lars S Rasmussen has no conflicts of interest. Thomas A Schmidt has no conflicts of interest. Janus C Jakobsen has no conflicts of interest.


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SOURCES OF SUPPORT

Internal sources • Faculty of Health and Medical Sciences, University of Copenhagen, Denmark. CS has received a PhD stipendium, this review will be part of the PhD project. • Region Zealand, Denmark. CS has received a PhD stipendium, this review will be part of the PhD project.

External sources • Tryg Foundation, Denmark. LS has received funding from Tryg Foundation for other projects. • Region Zealand Research Foundation, Denmark. CS has received a 10,000 euro grant for a PhD project, this review will be part of the project.

NOTES This protocol is based on standard text and guidance provided by the Cochrane Effective Practice and Organisation of Care (EPOC) Group.


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