Prospective 4-year follow-up of two randomised controlled trials using routine primary care data


Abstract

Methods and findings

Randomisation was from October 2012 to November 2013 for PACE-UP participants from seven general (family) practices and October 2011 to October 2012 for PACE-Lift participants from three practices. We downloaded primary care data, masked to intervention or control status, for 1,001 PACE-UP participants aged 45–75 years, 36% (361) male, and 296 PACE-Lift participants, aged 60–75 years, 46% (138) male, who gave written informed consent, for 4-year periods following randomisation. The following new events were counted for all participants, including those with preexisting diseases (apart from diabetes, for which existing cases were excluded): nonfatal cardiovascular, total cardiovascular (including fatal), incident diabetes, depression, fractures, and falls. Intervention effects on time to first event post-randomisation were modelled using Cox regression for all outcomes, except for falls, which used negative binomial regression to allow for multiple events, adjusting for age, sex, and study. Absolute risk reductions (ARRs) and numbers needed to treat (NNTs) were estimated. Data were downloaded for 1,297 (98%) of 1,321 trial participants. Event rates were low (<20 per group) for outcomes, apart from fractures and falls. Cox hazard ratios for time to first event post-randomisation for interventions versus controls were nonfatal cardiovascular 0.24 (95% confidence interval [CI] 0.07–0.77, p = 0.02), total cardiovascular 0.34 (95% CI 0.12–0.91, p = 0.03), diabetes 0.75 (95% CI 0.42–1.36, p = 0.34), depression 0.98 (95% CI 0.46–2.07, p = 0.96), and fractures 0.56 (95% CI 0.35–0.90, p = 0.02). Negative binomial incident rate ratio for falls was 1.07 (95% CI 0.78–1.46, p = 0.67). ARR and NNT for cardiovascular events were nonfatal 1.7% (95% CI 0.5%–2.1%), NNT = 59 (95% CI 48–194); total 1.6% (95% CI 0.2%–2.2%), NNT = 61 (95% CI 46–472); and for fractures 3.6% (95% CI 0.8%–5.4%), NNT = 28 (95% CI 19–125). Main limitations were that event rates were low and only events recorded in primary care records were counted; however, any underrecording would not have differed by intervention status and so should not have led to bias.

Introduction

Strong evidence exists that physical activity (PA) is protective for a wide range of health conditions [1–3], and inactivity is claimed to be the fourth leading risk factor for global mortality [2]. Meta-analyses of cohort studies have reported clear benefits of moderate-intensity PA for many chronic diseases, including diabetes [4], ischaemic heart disease [4], stroke [4], fractures [5], and depression [6]. However, all these estimates are based on evidence from observational cohort studies, in which individual baseline differences in PA levels, assessed by questionnaires, were linked to subsequent disease outcomes. PA questionnaires are known to be inaccurate and subject to recall bias [7], and there is the possibility of regression dilution bias in such studies, which would lead to underestimating benefits. This raises the question of whether changes in PA that occur after PA interventions will have similar or possibly larger effects. An additional advantage of trial data is that changes in PA have usually been objectively measured.

Many PA interventions, including pedometer-based walking interventions, have shown short-term increases in PA levels [8–10], but to achieve the long-term health benefits demonstrated above in cohort studies, increases in PA need to be sustained, and long-term trial data with objectively measured PA outcomes and robust health outcomes are limited, with calls for more such trials [10–12]. The Finnish Diabetes Prevention Study observed significant PA increases and showed impressive 58% reductions in type 2 diabetes, but it combined dietary and PA interventions; therefore, it is difficult to estimate independent PA effects [13]. In contrast, a recent large primary care trial failed to reduce type 2 diabetes incidence, despite increasing PA levels [14]. Trials examining PA effects on cardiovascular outcomes have shown mixed results: some showing strong protective effects on both heart attacks [15,16] and strokes [16] but others failing to reduce cardiovascular events [17]. Primary care trials that have successfully increased PA levels have shown both increased [18] and reduced [19] self-reported falls, but a systematic review of exercise interventions in older adults demonstrated a significant reduction in fall-related fractures [20]. A meta-analysis of PA interventions demonstrated a reduction in depressive symptoms [21]. However, only one of the trials above used routinely recorded primary care or hospital data to capture events [15]; for other trials, participants were asked about health events, and these were validated by checking patient records, leading to important potential reporting bias. The benefit of using routine electronic records for extended follow-up of trials has been established in a different context by the West of Scotland Coronary Prevention Study, which showed that routine records gave very similar results to rigorously collected clinical trial data for cardiovascular events and deaths [22]. Using routine records in trials has the additional merit that if participants have given permission to access their health records, these may be available even when participants are lost to follow-up.

We conducted two pedometer-based walking trials with adults and older adults (PACE-UP, PACE-Lift), which increased accelerometer-measured step count and moderate-to-vigorous PA (MVPA) levels in bouts at 12 months [23,24] and with sustained PA increases at 3–4 years [25]. Across both trials at 3–4 years, all intervention groups were doing approximately an extra 30 minutes per week of MVPA compared with baseline, up about a third on their baseline levels [25]. Both trials recruited through primary care, and participant consent to link trial data with primary care record data was sought. The aim of the present paper was to evaluate the intervention effects from PACE-UP and PACE-Lift on longer-term health outcomes relevant to the walking interventions, using routinely collected primary care data.

Methods

Study design and participants

Two primary care randomised controlled trials (RCTs) of effective 12-week pedometer-based walking interventions are included, both providing long-term health outcome data from routine primary care records: PACE-UP, which recruited 45- to 75-year-olds from seven London (United Kingdom) practices from October 2012 to November 2013, and PACE-Lift, which recruited 60- to 75-year-olds from three Berkshire and Oxfordshire (UK) practices from October 2011 to October 2012. The trials were similar in their primary care recruitment and in the 12-week pedometer-based walking interventions, incorporating behaviour-change techniques [26, 27]. Participants were very similar in terms of their baseline characteristics, apart from deprivation level (see Table 1), but randomisation ensured even distribution of deprivation levels across intervention and control groups [23,24], and deprivation was not an effect modifier [23]. At long-term follow-up, 3-year findings for both PACE-UP intervention groups (postal and nurse-supported) and 4-year findings from the PACE-Lift (nurse-supported) intervention group all showed very similar effects on PA levels [25]. Given the similarities of these trials and their sustained PA effects, we therefore present a combined analysis of all three intervention groups at 4 years on primary care outcomes. All analyses adjust for study as a covariate.

Procedures

We downloaded primary care data for trial participants who gave written consent, minus those who subsequently withdrew from the trials, for the 4-year periods following randomisation from the seven PACE-UP and three PACE-Lift practices. Data were downloaded at 12 months (at end of initial trial follow-up) and at 4 years (after extended follow-up) at all 10 practices. If participants had both sets of data, the 12-month data were not needed, as they were duplicated in the 4-year data. For those without any data at 4 years, 12-month data were used, if available. See CONSORT diagram (Fig 1) for details of numbers of participants at each time point with primary care data for both trials. Data on participants were censored if a patient left the practice or if they died whilst still registered at the practice. Searches were set up to download the following information from primary care records: Read codes for diseases (including those arising from hospital admissions) and consultation data (see S1 Fig for details of exactly how events were counted). For cardiovascular events and depression, we separated events occurring in participants with and without preexisting disease, so Read codes for these diseases that occurred prior to the individual randomisation date were taken as evidence of preexisting disease. Prior Read codes for diabetes were used to exclude those with preexisting diabetes at date of randomisation from subsequent diabetes analyses only, so that we could estimate numbers of new type 2 diabetes diagnoses. Data were processed blind to trial group, by a researcher without access to trial data apart from randomisation dates, according to an agreed protocol. Two medically qualified researchers, also blind to intervention group, separately checked that the events counted were appropriate. Details on deaths (including date and cause) were collected systematically for both trials from general practices prior to recontacting participants for long-term follow-up (at 3 years for PACE-UP and 4 years for PACE-Lift) and were therefore available for all participants for this period of follow-up (regardless of whether they had given permission for their primary care records to be downloaded), apart from any patients who had deregistered with their practice by moving away. Known deaths from cardiovascular causes were counted as outcome events and included in total cardiovascular events; other deaths were treated as censored data. Once all events had been verified, the primary care data and trial data were linked.

Results

Overall, 98% (1,297/1,321) of initial trial participants gave written consent for primary care data linkage and had their data downloaded—1,001/1,023 (98%) from PACE-UP and 296/298 (99%) from PACE-Lift at baseline—and 223/225 (99%) of PACE-Lift participants recontacted at 4-year follow-up. Primary care data available at different time points are shown in the two flow diagrams (Fig 1a and 1b). Overall, 82% (1,077/1,321) of participants had 4 years of complete data: 85% (871/1,023) of PACE-UP and 69% (206/298) of PACE-Lift participants.

Table 3 presents the time to first event for each outcome; the model coefficients are given in S1 Table. For nonfatal cardiovascular events, in both trials the proportion of events was lower in the intervention than in the control group, both for those without a prior cardiovascular diagnosis and for all participants. The hazard ratios for all participants were 0.24 (95% CI 0.07–0.77, p = 0.02) (demonstrated in a Kaplan-Meier plot in Fig 2) and for those without a prior diagnosis 0.27 (95% CI 0.08–0.88, p = 0.03). When fatal cardiovascular events were included, results were similar: hazard ratios of 0.34 (95% CI 0.12–0.91, p = 0.03) for all participants and 0.31 (95% CI 0.11–0.93, p = 0.04) for those without a prior diagnosis. In terms of new diabetes diagnoses, there was no statistically significant intervention effect, with a hazard ratio of 0.75 (95% CI 0.42–1.36, p = 0.34). Similarly, for new depression diagnoses, there was no overall effect of the intervention, hazard ratio 0.98 (95% CI 0.46–2.07, p = 0.96) in all participants and 0.92 (95% CI 0.41–2.03, p = 0.83) in those without a prior diagnosis. For fractures, in PACE-UP the proportion of patients with a fracture during follow-up was lower in the intervention group (26/668, 3.9%) compared with the control group (28/333, 8.4%); for PACE-Lift both groups had similar proportions of fractures, 5.4% (8/149) in the intervention group and 5.4% (8/147) in the control group. The overall Cox regression hazard ratio across both trials was significantly reduced (0.56, 95% CI 0.35–0.90, p = 0.02). Fig 2 also shows these findings in a Kaplan-Meier time-to-first-event diagram.

Table 4 shows the findings for medically reported falls and consultations; S1 Table shows the coefficients. Overall, approximately 14% (115/818) of intervention and 13% (63/480) of control participants had one or more falls during follow-up; the overall incident rate ratio for falls was 1.07 (95% CI 0.78–1.46, p = 0.67). The mean number of consultations per year over 4-year follow-up was similar in intervention and control groups for both trials (approximately 6, with a standard deviation of 5), and the incident rate ratio was 1.01 (95% CI 0.93–1.10, p = 0.82), showing no intervention effect on number of consultations.

Table 5 shows the ARRs and NNTs (95% CIs) for each event, combined across both trials. The results for cardiovascular events and fractures (for which our interventions were associated with a protective effect) for all participants were as follows: nonfatal cardiovascular events ARR 1.7% (0.5%–2.1%), NNT 59 (48–194); total cardiovascular events ARR 1.6% (0.2%–2.2%), NNT 61 (46–472); fractures ARR 3.6% (0.8%–5.4%), NNT 28 (19–125).

Discussion

Strengths and weaknesses of the study

Important strengths were that both trials recruited from primary care and that we sought participant consent to use their primary care data, thus allowing us to examine long-term health outcomes using routinely collected data. Having two trials with similar recruitment methods and interventions, which we had previously combined for long-term follow-up [25], meant that we increased the power of our analyses. A key strength of UK routinely recorded primary care data, which may not apply to other healthcare systems, is that it fully captures secondary care diagnoses from accident and emergency, outpatients, and hospital admissions (National Health Service and private), in addition to primary care consultations and diagnoses, thus reducing potential for bias in outcome assessment. The inevitable losses that occur when collecting long-term trial follow-up data can be reduced by using routinely collected data for outcome assessment. We followed up 67% (681/1,023) of participants at 3 years in PACE-UP [25] and 76% (225/298) at 4 years for PACE-Lift with objective PA primary outcome data, but for these analyses using routinely collected primary care data at 4 years, we had 98% (1,297/1,321) contributing to analyses and 82% (1,077/1,321) providing complete data over the whole 4 years, despite needing to reconsent PACE-Lift participants at 4-year follow-up. Others have shown how higher levels of electronic follow-up (93%) compared with fieldwork follow-up (83%) at 2 years retained more of those in the most deprived groups [35], demonstrating reduced potential for selection bias.

An important limitation is that we did not have complete 4 years of follow-up data for all participants; however, differences were already evident in cardiovascular events and fractures by 12-month follow-up, when we had over 97% complete primary care data across all groups. We were also constrained by the data routinely recorded in primary care records, which do not reflect all cases. For cardiovascular events and fractures, underrecording is unlikely to have been a problem, as major diagnoses like myocardial infarction, stroke, coronary artery bypass graft, fractures, etc., are well recorded in primary care records following hospital notification of events. For falls and new depression episodes, cases occurring in the community but not reported to primary care will be missed, and for diabetes, new cases are only diagnosed when blood tests are done. However, although cases will be underrecorded in primary care records for these conditions, there is no reason for this to differ by intervention status, particularly as the intervention did not affect consultation rate, so this should not have led to bias. A further limitation is the uncertainty of our estimates. Given the low event rate in this sample and the relatively short follow-up period for events, the CIs are wide, indicating uncertainty regarding the exact magnitudes of effect.

Comparisons with previous studies

Details of all the intervention studies that are referred to in this section, including more information on the specific interventions and their effects on PA levels, are summarised in S2 Table.

Cardiovascular events.

The reductions we demonstrated in nonfatal (0.24 [95% CI 0.07–0.77]) and total (0.34 [95% CI 0.12–0.91]) cardiovascular events are consistent with the effect in older primary care patients 2 years after a 9-month PA programme that significantly increased self-reported PA and significantly decreased blood pressure and lipids (reduction in cardiovascular events risk ratio 0.15 [95% CI 0.04–0.51]) [15]. Similarly, others showed significant reductions in both heart attacks (relative risk 0.51) and strokes (relative risk 0.52) alongside self-reported PA increases, 6 months post-intervention in community-based hypertension patients [16]. However, Newman et al found no cardiovascular event reduction in the PA group at 2.6-year follow-up in older adults with functional limitations (hazard ratio 1.10 [95% CI 0.85–1.42]) [17]. Possible reasons were that the PA intervention group had more opportunity to report events; cardiovascular disease levels were high, possibly precipitating events or reducing potential benefits; and there was a possible suboptimal activity dose, as their moderate PA cutoff was >760 counts/minute [17], much lower than ours (≥1,952 counts/minute) [26, 27].

Comparisons with risk estimates from cohort studies are more difficult. A key issue is that all cohort studies in systematic reviews are based on questionnaire PA measures, with their known inaccuracies and recall bias [7]; the variety of different questionnaires also makes it difficult to standardise how PA is quantified. Cohort studies’ effect estimates usually compare inactive participants with those achieving much higher PA levels. Thus, a recent good-quality systematic review provides relative risks for an 11.25 metabolic equivalent (MET) hour/week increase in PA levels compared with being inactive of 0.69 (95% CI 0.67–0.71) [36], corresponding to international recommendations of 150 minutes of MVPA weekly in ≥10-minute bouts [37]. Our intervention increased PA by about 30 minutes of MVPA in bouts weekly long-term, one-fifth of 150 minutes, so after scaling down the relative risks from that paper [36] (S5 Text), their cardiovascular incidence effect estimate for the same level of PA increase becomes 0.98 (95% CI 0.97–0.99), suggesting a much more modest effect on cardiovascular events than from our intervention study.

Depression.

We found no intervention effect on new depression cases (hazard ratio 0.98 [95% CI 0.46–2.07]), although CIs were very wide. A systematic review and meta-analysis of PA interventions reported reduced depression symptoms (standardised mean effect size 0.37 [95% CI 0.24–0.50] for supervised PA studies and 0.52 [95% CI 0.28–0.77] for unsupervised studies) [21], supported by a systematic review of exercise referral schemes, which also showed reduced clinical depression risk in the two studies reporting this outcome (pooled standardised mean difference −0.82 [95% CI −1.28 to −0.35]) [41]. Of note, most studies included in the reviews reported depression risk based on symptom scores rather than clinical diagnoses of depression; we extracted the latter from primary care records, which could underestimate depression risk, as it relies on patients presenting with symptoms and general (family) practitioners detecting and recording them. Our negative finding from primary care records is, however, consistent with our main trial outcomes, which showed no intervention effects on depressive symptoms at 12 months [23, 24] or 3–4 years [25].

Cohort studies support an association between PA levels and depression, with increased PA levels associated with reduced depression risk, with the majority of studies (25/30) in a systematic review reporting this, though no meta-analyses or forest plots were presented [42], so there is no overall effect estimate for direct comparison with our findings.

Implications for clinicians, researchers, and policy makers

An important implication for both future clinical practice and policy is that primary care short-term pedometer-based walking interventions incorporating behaviour-change techniques can lead not only to long-term changes in PA levels but also to long-term beneficial health effects for adults and older adults. They could thus help to address the public health physical inactivity challenge and be part of the ‘call to activity’ for clinicians and patients [43]. This supports current guidance to promote pedometers alongside support for goal-setting, self-monitoring, and feedback [44] and suggests that policy makers should consider investment in this short-term primary care pedometer-based walking intervention because of its proven long-term health benefits. Our previous work has shown that sustained effects on PA levels were similar for postal and nurse-supported intervention groups [25] and that the postal route was more cost-effective [28]; this route therefore seems most promising to pursue for implementation.

Our demonstration of the widespread acceptance by trial participants for their primary care records to be accessed and the feasibility of using these data for evaluating long-term health outcomes is consistent with others’ findings [22, 35]. Our experience supports initiatives from funders such as the Medical Research Council and the National Institute for Health Research in the UK and other funders internationally, to encourage researchers undertaking trials to include options for longer-term data collection from routine records in their funding applications. We found only one other example of a PA trial that used routine primary care data to assess long-term health outcomes [15]. Using such outcomes provides objective evidence applying to all those randomised (not just those who complete trial follow-up), and by focusing on the clinical benefits, it also avoids the problems inherent in measuring change in PA levels in large numbers of subjects. Linking healthcare data to trial data can strengthen the evaluation and implementation of primary care–based interventions and should be more widely explored by researchers.

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