Interdisciplinary collaboration across secondary and primary care to improve medication safety in the elderly (The IMMENSE study) – a randomized controlled trial

This is a parallel group non-blinded RCT with an intervention group and a control group (1:1 ratio). Study enrollment started in September 2016 and ended in December 2019. All patients were followed up for 12 months after hospital discharge.

The trial was conducted in compliance with the published study protocol [24], the principles of Good Clinical Practice and the Declaration of Helsinki and is reported according to The Consolidated Standards of Reporting Trials (CONSORT) reporting guideline and template for intervention description and replication (TIDieR) checklist [24‐27].

The study was carried out at a geriatric internal medicine ward and a general internal medicine ward at the University Hospital of North Norway (UNN). The geriatric ward cares for older patients with complex acute medical needs, and physicians are specialized in geriatric medicine. The general medicine ward treats patients admitted for stroke, pulmonary-, kidney- and endocrine diseases as well as patients with geriatric concerns. Pharmacists were not involved in standard patient care at the study wards.

Inclusion criteria were acutely admitted patients aged ≥ 70 years and willing to provide written informed consent (patient or next of kin). Patients were excluded if they had been admitted to the study ward more than 72 h before evaluation of eligibility, moved to and discharged from other wards during the index stay, unable to understand Norwegian (patient or next of kin), considered terminally ill or with a anticipated short life expectancy, were planned discharged on the inclusion day, occupying a bed in a study ward but under the care of physicians from a non-study ward, or if intervention from a study pharmacist was considered necessary for ethical reasons (before randomization or in the control group). Readmitted study patients were not re-included due to limited pharmacist resources, but received standard care. Patients referred to a patient-centred care team project upon discharge, including pharmaceutical care, were not excluded.

Patients were screened for eligibility and recruited by study pharmacists. Enrolment and clinical work were performed from 8.00 am—3.30 pm on weekdays. In the geriatric ward, the study pharmacists were present every weekday, but only every other weekday in the general medicine ward. Patients were approached for inclusion in a predetermined order to avoid selection bias.

After collecting baseline data, patients were randomized by study pharmacists using a web-based service supplied by the department of applied clinical research at the Norwegian University of Science and Technology. The randomization block sizes were permuted, of unknown and variable size and stratified by the study site. As pharmacists were only involved with patients in the intervention group, blinding of group allocation for patients, pharmacists, and the interdisciplinary team was impossible. However, the primary analysis was performed by an investigator not involved in the data collection and blinded for group allocation (KS).

The intervention was based on the IMM model, including a pharmacist in the interdisciplinary ward team working closely with the patients, physicians, and other team members [24]. Briefly, the five-step IMMENSE intervention comprised medication reconciliation, medication review, medication counselling, transmission of medication information upon discharge and finally, oral communication with primary care after discharge, see Table 1. Control group patients received standard care, which was care from the same ward team, except the services provided by the pharmacist. Six pharmacists were involved in delivering the intervention throughout the study period, all holding master's degrees in pharmacy and trained in the IMM study procedures.

The primary outcome was the rate of emergency medical visits 12 months after discharge from the index hospital stay, an endpoint relevant both for patients and health care systems, previously shown to be affected by similar interventions in similar health care systems, e.g. in the study by Gillespie et al. [28]. Emergency medical visits is a composite outcome of acute readmissions and ED visits. We defined acute readmissions as any subsequent admission following the index stay, excluding elective readmissions. ED visits included emergency visits to the hospital and visits to municipality-run emergency medical clinics if the patients were not subsequently admitted to the hospital. A prespecified secondary analysis of the time to reach the primary outcome and the proportion of patients reaching the primary outcome was performed.

Secondary outcomes included i) the length of index hospital stay ii) time to first acute readmission, iii) the proportion of patients readmitted acutely within 30 days and iv) mortality rate during 12 months of follow-up. Other prespecified outcomes relating to inappropriate prescribing, medication-related readmissions and health-related quality of life specified in the study protocol will be addressed in future articles.

Baseline data collected: age, gender, marital status, level of education, type and amount of help from home care services, delivery of multi dosage dispensed medications, medical diagnosis/medical history, and medication use at the time of hospital admission. Data was registered in a Microsoft® Access database which has been the basis for previously reported data on intervention fidelity and process data on identified MRPs [29].

Data on outcomes was collected from national health registries; readmissions and hospital ED visits from The Norwegian Patient Registry, emergency medical visits to EDs run by local municipalities from The Norwegian Health Economics Administration Registry, and deaths from the National Cause of Death Registry [30]. Linking data was possible through the unique personal identification number assigned all Norwegian citizens. An ED visit within the six-hour window before a hospital stay was counted as a hospital stay only. We collected registry data from 12 months before and 12 months after the index stay to enable adjustments for pre-study risk factors.

Sample size calculation for the primary outcome was based on the study by Gillespie et al. applying the same composite endpoint [28]. This trial investigated the effectiveness of a multifaceted intervention including post-discharge interventions performed by ward-based pharmacists in reducing morbidity and hospital visits among patients 80 years and older. They randomized 400 patients in a 1:1 relationship and found a 16% reduction in all-cause visits to the hospital in the intervention group. We estimated a rate of acute hospital admissions and ED visits of 1.7 per year in our patient population. Consequently, we needed to enrol 456 patients (228 in each group) to detect a 16% reduction in hospital visits with a 5% significance level and 80% power. Taking dropouts into account, we aimed to include 250 patients in each group. We extended the enrollment period three weeks after reaching 500 patients to compensate for exclusions.

Data was analyzed by an intention-to-treat (ITT) principle but modified as registry data on endpoints were unavailable for patients who withdrew the informed consent. We also excluded patients dying during the index hospital stay from the analysis. The statistical analysis plan (SAP) can be found in Supplement 1. A prespecified per-protocol (PP) analysis, including patients not excluded after randomization, was also performed.

The primary analysis was a multilevel Poisson regression to handle clustering on the study ward level and repeated measurements on the patient level. We applied time out of hospital alive (days at risk of an event) in the 365 days after discharge as an offset and adjusted for the number of emergency medical visits in the 365 days prior to the index hospitalization.

Time to first readmission and time to first emergency medical visit was analyzed by the Kaplan–Meier method and the log-rank test. A Cox proportional Hazards Model (adjusted and unadjusted) was applied to estimate hazard ratios (HRs), which are presented with 95% confidence intervals (CIs). The differences in lengths of stays between groups were assessed with an independent sample Mann–Whitney test. The differences in proportions of patients alive at 12 months and patients readmitted within 30 days were compared with logistic regression (adjusted and unadjusted). A two-sided alpha level of 5% with no adjustments for multiplicity was used as a statistical significance level.

The effect of the intervention on the primary endpoint was explored in the following prespecified subgroups i) number of medications upon admission or discharge; 0–5, 6–10, > 10, ii) age groups; 70–80, 80–90 and > 90, iii) patient responsible for their own medication after discharge; yes, no, partly, iv) Charlson Comorbidity Index score; 0–2, > 2, v) the number of hospital visits in the 12 months prior to inclusion; 0–1, > 1, vi) length of hospital stay; 0–6 days, > 6 days, vii) living status before hospitalization; referred from home, home-care or nursing home, and viii) ability to self-provide informed consent or not.

The multilevel Poisson regression was performed in STATA® 16.1, data management and the remaining analyses in IBM® SPSS Statistics Version 28.

This study has several strengths such as the randomized controlled design to create comparable study groups and control for bias, and the blinding of the investigator performing the primary analyses. Furthermore, the Norwegian health registries enable a complete and quality assured collection of outcomes. The collection of data for the 365 days prior to the index hospital stay, enabled us to adjust for pre-study patterns. This was important as the control group seemed to be somewhat sicker at baseline and controlling for the rate of the primary endpoint in the year prior gave strength to the analysis. Finally, including patients with dementia and cognitive impairment, increase the generalizability of findings.

There are also limitations that need to be addressed. First, intervention and control patients were included from the same wards and cared for by the same health professionals, which may have introduced a contamination bias, reducing between-group differences. This could have been prevented by including more wards and performing cluster-randomization, but was not practically possible due to limited funding. Second, the inclusion rate was slow as the pharmacists were only able to include a limited number of patients each day due to the workload associated with study-related tasks and delivering the intervention [47]. Consequently, a small proportion of admitted patients were screened for eligibility or asked for participation, possibly introducing a selection bias. To prevent selection bias, the study pharmacists always approached patients in a predetermined order (last-admitted-asked first). Third, due to a slow inclusion rate, the enrollment period lasted for three years, which enabled changes in standard care at the wards related to medication management, e.g., new methods for medication reconciliation. How changes in standard care may have influenced the study results is unknown, however it does not seem very likely from our post-hoc analyses. Fourth, our study was powered to investigate a possible difference in number of events after one year. In retrospect, we recognize that the intervention was probably underpowerd to identify a more likely effect on short-term event rates. Finally, due to the complexity of the intervention, not all intervention steps were delivered to all patients, and whether recommendations were followed-up upon in primary care is unknown [29]. A process evaluation alongside the trial could have enabled the identification of barriers and enablers to the effective delivery of the intervention, which would have provided valuable information on how to develop better interventions in the future [48].