The trial protocol has been described by Bower and colleagues.13
Initial discussions with sites indicated that individual randomisation of patients would probably not be acceptable to stakeholders. Therefore, we used a pragmatic approach to randomise general practices. Participants in practices allocated to the control group were given usual care, which reflected the range of services available in the trial sites, excluding telehealth, and were offered telehealth or telecare at the end of the trial, if they were still eligible at that point.
Choices of telehealth devices and monitoring systems varied among the three trial sites, and there was no attempt to standardise these technologies across sites. We included a broad class of technologies, and the study was not designed or powered to examine differences between specific devices or monitoring systems. Although sites used different protocols for allocating peripheral devices, they all used a pulse oximeter for chronic obstructive pulmonary disease, a glucometer for diabetes, and weighing scales for heart failure. Sites asked participants to take clinical readings at the same time each day for up to five days per week, although the frequency was adjusted according to their individual history. For example, a participant with diabetes and well controlled blood glucose would be asked to take readings less frequently than another participant with poorly controlled blood glucose.
In addition to the telemonitoring aspect of the intervention, symptom questions and educational messages were sent to participants either via the telehealth base unit or via a set top box connected to a television. At the end of each session, data from clinical readings and symptom questions were transmitted to monitoring centres via a secure server. Monitoring centres were staffed by specialist nurses and community matrons from local health organisations, who used protocols to respond to the information from patients.
All practices in the geographical areas covered by three study sites (Cornwall, Kent, and Newham in England) were eligible to participate in the trial. Practices that accepted the invitation to participate were allocated to an intervention or control group via a centrally administered, minimisation algorithm that aimed to ensure that the groups of practices were similar in terms of practice size; deprivation index; proportion of non-white patients; prevalence of diabetes, chronic obstructive pulmonary disease, and heart failure; and site. Within each practice, patients aged 18 years or over were deemed eligible on the basis of a diagnosis in primary or secondary care of chronic obstructive pulmonary disease, diabetes, or heart failure. We did not confer eligibility on the basis of formal clinical assessment of disease severity. Instead, patients were deemed eligible on the basis of their inclusion on the relevant Quality Outcomes Framework register in primary care; a confirmed medical diagnosis in primary or secondary care medical records, as indicated by general practice Read codes or ICD-10 (international classification of diseases, 10th revision) codes; or confirmation of disease status by a local clinician (a general practitioner or community matron) or the patient’s hospital consultant. We did not exclude patients on the basis of additional physical comorbidities.
To meet ethical obligations, sites asked patients to complete and return a data sharing letter if they consented to their data being shared with the research team. Once this letter had been returned, patients received a “light touch” visit from members of the site project team, sometimes including clinical staff. These visits aimed to assess the suitability of the patient’s home for telehealth, provide information regarding the trial, and provide consent forms for participation. The study design required that patients were blinded at the point of consent. However, owing to the large sample size needed for the trial and the extended period of recruitment, it was not possible to guarantee the blinding of recruiters to the allocations of general practices throughout the process.
We assessed the effect of telehealth at the patient level. The primary endpoint was the proportion of people with an inpatient admission to hospital within the 12 month trial period. The study was powered on the basis of detecting a relative change of 17.5% from a baseline of 25% (from a priori site estimates), at 80% power, and a two sided value of P<0.05. Previous studies in the older population suggested that the intracluster correlation coefficient would be about 0.001.14
We did sample size calculations using the appropriate formulas,15
and found that 3000 patients would need to be recruited (25 patients from each of 120 general practices). We examined mortality over 12 months and prespecified secondary endpoints (including the number of inpatient bed days, emergency admissions, elective admissions, outpatient attendances, and emergency department visits, as well as the notional cost of hospital activity to commissioners of care based on national tariff costs).
Participants were linked at the person level to data for inpatient and outpatient secondary activity sourced from Hospital Episode Statistics, a national data warehouse for England.16
Participants were linked by the NHS Information Centre for health and social care, a trusted third party that was the only organisation to have access to both patient identifiers and data for secondary care activity. A linked mortality file provided data for all deaths occurring in and out of hospital. In addition, participants were linked to local commissioning datasets on visits to emergency departments, which included all visits to emergency department and not just those that resulted in an admission, and to general practice datasets. In these data, patient identifiable fields were removed before transfer and NHS numbers encrypted. We used this encrypted NHS number to link participants to the emergency and general practice data.
We restricted analysis of inpatient activity to ordinary admissions, and excluded transfers, regular ward attendances, and maternity events (leaving patient classifications 1 and 2 only). Admissions were classified by defined admission methods into emergency activity (codes 21-28) and elective activity (all other codes excluding transfers). Bed days included stays after emergency and elective admissions; same day admissions and discharges were assigned a stay length of 1 bed day. We restricted outpatient activity to appointments that were attended (codes 5 and 6).
A separate paper is planned to detail the effect of telehealth on costs. Here, we included notional costs of hospital care to summarise overall levels of hospital use in the intervention and treatment groups across the inpatient and outpatient categories. We estimated notional costs of care, from Hospital Episode Statistics data, by applying the set of mandatory and indicative tariffs used in England for the reimbursement of inpatient and outpatient care (2008-09 payment by results tariffs).17
These tariffs assume a stay of a certain number of days (the “trim point”), and allow hospitals to charge a prespecified amount for each additional excess bed day. Costs were not adjusted for the regional costs of providing care, and thus were effectively a weighted activity measure that allowed robust comparison of the magnitude of care received for control and intervention participants. We did not include costs for activity not covered by the tariffs, such as mental health, critical care, cystic fibrosis, high cost drugs, and outpatient physiotherapy.
The current study was restricted to those patients linked to administrative data who began the trial before 30 September 2009. The trial start date was taken as the date of telehealth installation for intervention patients, and as the date of the “light touch” visit for control patients. Analysis was based on comparing activity over 12 months after this date, at the person level.
Analysis of participants was on the basis of the intended treatment allocations, and regardless of subsequent withdrawal from the trial. For randomised trials, formal statistical tests on the similarity of intervention and control patients have been thought to be inappropriate, since allocations are known to have been random.18
However, in cluster randomised trials, selection bias is theoretically possible, either through systematic differences between practices in the control and intervention groups, or because of similar differences at the individual level.19
We presented standardised differences as a summary measure of differences between groups; we calculated a standardised difference as the difference between the sample means (or proportions), divided by the pooled standard deviation.20
Although various aspects of the trial design mitigated against the risk of selection bias, differences between groups could still have occurred by chance. We applied case mix adjustment using three models to account for the effect of any differences between groups (box).
Box: Models used for case mix adjustment
The simplest models, although accounting for the effect of clustering, used no additional covariate adjustment.
A more complex model additionally controlled for residual imbalances in a set of characteristics predictive of future hospital use. These characteristics included age, sex, ethnicity, site, number of chronic health conditions, principal long term condition (diabetes, chronic obstructive pulmonary disease, or heart failure), an area based deprivation score (national quartiles of the index of multiple deprivation 2007), and a metric corresponding to the endpoint calculated over several periods within the two years before recruitment. The number of chronic health conditions was a count of diagnoses recorded on inpatient data over the three years before starting the trial. We assigned principal long term conditions using a pragmatic approach according to published criteria.13
More complex case mix adjustment was conducted using the combined model.11
This model is a standard instrument designed to estimate the probability that an individual would be admitted to an emergency hospital department within a 12 month period. The combined model score accounts for 72 variables related to age, sex, recorded health conditions, previous hospital use, and prescriptions. These variables are sourced using administrative data from general practices as well as from local hospital commissioning datasets.
The combined model was originally derived using data for 2002-05;11
we revalidated its performance on more recent data covering the period from April 2007 to March 2009. Revalidation used data extracted for the trial sites excluding trial participants. For the case mix adjustment, we calculated the combined model score for each participant at the end of the month before the start date. If a general practice did not grant approval for us to extract data, we imputed scores for patients on the basis of the available information, which included age, sex, and hospital data. We used single imputation on the basis of linear regression on the logit scale.
In a cluster randomised trial, hospital use for individuals in the same general practice will tend to be correlated. We accounted for this degree of clustering by constructing multilevel models that included random effects at the practice level. Logistic regression was used for the admission proportion and mortality, with the exponent of the coefficients used to calculate odds ratios. For emergency admissions, elective admissions, outpatient attendances, and emergency department visits, we used Poisson regression and exponentiated the coefficients to produce incidence rate ratios. Distribution of healthcare costs and hospital bed days are typically skewed, with some very large values and a considerable proportion of the population at zero. Although opinions differ on how to analyse such data,21
we incremented and log transformed notional costs and bed days to meet the assumptions needed for subsequent ordinary least squares modelling. Model coefficients were exponentiated to calculate geometric mean differences. We did all analyses in Stata 11.22
The primary analysis assumed a 12 month follow-up for all patients, regardless of whether they died or not. This tested for differences between the groups in overall levels of hospital activity after the introduction of telehealth. However, clinicians and other healthcare professionals might also be interested in how telehealth would affect patients’ experiences of admission to hospital, which would depend on whether they were alive at that point. Such effects may be different if telehealth affected the mortality rate. Therefore, we did secondary analyses to assess group differences in admission rates at any point in time, on the condition that participants were alive just before that point in time and had not already been admitted. This analysis treated death as a form of statistical censoring and used the Kaplan-Meier curve.23
Although the Kaplan-Meier curve did not take into account differences between intervention and control groups at baseline, we also estimated the corresponding adjusted hazard ratio. We calculated hazard ratios using a Cox proportional hazards model,24
which included covariate adjustment according to the set of baseline variables (box) and random frailties to allow for homogeneity within practices.25