Summary of main findings
Within the intervention group, only 22% of participants were awarded extra financial or non-financial benefits after receiving domiciliary welfare rights advice: the remainder declined the advice, were awarded no benefits or declined the benefits for which they were eligible. Quantitative analyses found little evidence that domiciliary welfare rights advice led to positive impacts on HRQoL over the 24-month follow-up period. There was no significant difference in the primary outcome (CASP-19 score) between intervention and control group participants at 24 months (adjusted mean difference 0.3, 95% CI –0.8 to 1.5), nor was there evidence that the difference varied among subgroups distinguished by age, sex or socioeconomic position. We did find a significant change in the hours of care received per week, which increased more in the intervention group (53.7 vs. 42.0; adjusted difference of 26.3 hours/week, 95% CI 0.8 to 56.1 hours/week), but at the lower end of the CI the difference was of questionable value, while at the upper end of the CI the difference would be of real importance. This range reflected the small numbers receiving care, and the large variation between them in terms of hours of care.
Exploratory analyses indicate that there were no significant differences in primary or secondary outcomes between those in the intervention group who received welfare rights advice versus those who did not, and those in the intervention group who received benefits versus those who did not, excepting that those who did not receive benefits reported significantly higher levels of physical activity at 24 months. We also found no significant differences in CASP-19 score between the 55 participants in the intervention group who were awarded financial benefits compared with the 48 in the control group who were awarded financial benefits after 24 months and were thus comparable on eligibility (adjusted mean difference in CASP-19 score 1.4, 95% CI –2.0 to 4.7). We found no evidence of a dose–response relationship between amount of financial benefit received by those in the intervention group and change in CASP-19 score at 24 months. We did, however, find a weak positive correlation between CASP-19 score at 24 months and the amount of time since receipt of the benefit (0.39, 95% CI 0.16 to 0.58).
The qualitative data suggested that receipt of the intervention was acceptable, and both participants and professionals perceived the receipt of additional financial and non-financial benefits to have had a positive impact on health and HRQoL. For example, for some participants, the increased benefits allowed them to escape a stressful and precarious financial situation; prevented the need to borrow or reduce savings and helped to reduce debt, thereby increasing financial security and reducing stress; alleviated some food and fuel poverty and provided security against otherwise catastrophic unplanned costs; helped to maintain mobility, independence and pay for formal and informal support with activities of daily living; or allowed the provision of monetary or non-monetary gifts for informal help received, increasing perceptions of self-worth and reinforcing informal support networks. Overall, the picture painted by the qualitative findings was one that suggested that the intervention, when leading to additional financial or non-financial benefits, resulted in improvements in HRQoL with the potential to impact on physical or mental health, and could lead to increased independence.
The economic evaluation indicated that, on average, the delivery of domiciliary welfare rights advice was found to be more costly and more effective than standard practice. The average total cost per participant was £44 over 24 months. This included around £17 (95% CI £15 to £19) for additional activities associated with the intervention being delivered in participants’ homes. The mean health gain, although not statistically significant, from the Do-Well intervention after 24 months was 0.009 (95% CI –0.038 to 0.055) QALYs (adjusted for baseline EQ-5D-3L, age and gender), resulting in an ICER of £1914 per QALY gained. However, the probability that the intervention was cost-effective was only 60% when compared with conventional thresholds for society’s WTP for a QALY (£20,000) and any value above. For the majority of financial and non-financial benefits, including aids and adaptations, no difference in the number of new awards was observed between the trial arms over the study period. Using a cost–consequences analysis, from an individual perspective the value of the receipt of benefits was a gain, albeit one that did not clearly translate into improved health over the 2-year time horizon of the study. Imprecision around all estimates was high, and analyses involving multiple imputation to account for missing data yielded differing conclusions, indicating the degree of uncertainty that still exists.
Overall, the economic analyses showed that, despite no significant difference in quality of life being identified, changes in the receipt of benefits might be expected to impact on recipients’ well-being. Nevertheless, there was no evidence of any difference in welfare benefits between the trial arms, although CIs were wide enough to include potentially important differences. Even small increases in relatively small incomes might, therefore, be important.
Strengths and limitations of the study
This is the first RCT to examine the impact of welfare rights advice on health outcomes, and the first to explore specifically the impact of the advice on older people when it is delivered in their own homes. The trial was rigorously, ethically and legally conducted to internationally accepted standards, adhered to accepted reporting protocols and was overseen by an independent TSC. We employed rigorous controls to ensure data quality, and blinding to minimise bias among data collectors. Our primary and secondary outcomes were measured using validated scales, and were chosen on the basis of rigorous pilot work. We demonstrated the potential of the CASP-19 scale to show a clinically important change over time in relevant groups in advance of the trial using analysis of national cohort study data. The study was then powered to be able to demonstrate such a change as a result of the intervention. The intervention and control groups were balanced on all variables, indicating appropriate and effective randomisation.
The trial included a detailed process evaluation with both quantitative and qualitative components providing data that helped to explain the main trial and economic evaluation findings. We optimised the intervention prior to delivery by providing information, training and guidance for WRAs and GPs on their respective roles in ensuring welfare entitlements. We then assessed the fidelity of the intervention by recording and analysing a sample of WRAs’ interactions with clients. We were able to record only seven interactions. Although it is possible that WRAs who were not recorded delivered the service in a different way, resulting in systematically different outcomes, we think that this is unlikely, as a key performance indicator for WRAs is income maximisation, and they are therefore highly motivated to identify eligibility.
The qualitative study was rigorously conducted, with systematic and independent double coding of data to enhance internal validity. The participant data was corroborated using data from professional participants, and triangulated with our pilot study data.
The economic evaluation was conducted from public sector and Treasury perspectives, and comprehensively explored the potential for cost-effectiveness using both cost–utility and cost–consequences analyses. Sensitivity analyses assessed the impact of different data sources and varying key assumptions and parameters on the cost-effectiveness of the intervention.
We intended to conduct the trial in all local authority areas in one region, but found that two out of 12 authorities were unable to provide domiciliary welfare rights advice services, and in a further two local authority areas we were unable to recruit any general practices willing to participate. In the eight local authority areas in which we found willing general practices, there was variation in the ability or willingness of these practices to recruit participants, such that numbers of potential participants who were approached varied from 330 to 695 by local authority area and from 100 to 387 by general practice. Initial recruitment fell short of our target, and a second wave of recruitment, involving the recruitment of additional general practices, was necessary, which required us to seek an extension to the study. We recruited participants from general practices located in areas in the lower two-fifths of the distribution of socioeconomic deprivation, measured using the IMD 2010, using the method described by Griffin et al.72 However, when we examined the IMD scores assigned to the 17 general practices that agreed to participate in the study, the practices were in fact slightly less deprived on average [mean IMD score at MSOA level 37.0 (SD 10.4)] than the remaining 363 general practices in the North East [mean IMD score at MSOA level 38.5 (SD 11.5)]. Forty-five per cent of older people who were identified by general practices, and who did not opt out after receiving the initial invitation, later declined to participate. We have no information on these 1770 older people, who might have differed significantly (e.g. in terms of benefit eligibility or health status) from those who later participated. Similarly, of the 2142 we invited to participate, only 35% agreed to be randomised. Compared with those who declined, those who participated were, on average, less likely to be socioeconomically disadvantaged [IMD score at LSOA level 33.5 (SD 17.9) vs. IMD score at LSOA level 29.0 (SD 16.0)] and more likely to be women (50.5% vs. 53.5%). Overall, the recruitment rate varied from 8.5% to 26.0% (mean 19.3%; 755/3912) by general practice; it is unclear if this had an impact on outcomes. We compared these data with both the ELSA cohort and equivalent data from our pilot study. In both cases these data suggest that our trial cohort was somewhat more affluent than expected, which is likely to have reduced their eligibility for benefit outcomes and may, to an extent, explain the lower than expected proportion gaining additional benefits.
Participation in the study was limited to those fluent in English, which is likely to have excluded some older people from black and minority ethnic communities. Compared with the rest of the UK, the North East has a lower proportion of people from black and minority ethnic communities. The cost and complexity of providing translation and interpretation services for the very small number of participants (both for the trial and, in particular, for the domiciliary intervention) were considered too great to facilitate the participation of this group. Nevertheless, six people from black and minority ethnic groups participated in the trial (about 0.75% of participants). This does limit the generalisability of the study to black and minority ethnic populations in the UK. The study also excluded individuals deemed unable to participate in the research owing to poor mental or physical health, as assessed by their GP. In studies of this kind, it is usual for GPs to be offered the opportunity to exclude patients from the research who they feel would be unable to participate, or for whom the research might prove too challenging either physically or mentally. Nevertheless, such patients might have benefited from the intervention, and their exclusion may limit generalisability. The exclusion of the above groups may have contributed to the less socioeconomically disadvantaged profile of the trial participants.
One local authority did not deliver its own welfare rights advice services and, instead, contracted such services out to a third-sector organisation. In addition, during the course of the study there was substantial turnover of WRAs and changes in the local authority services available, which may have impacted on intervention delivery. For example, there was an indication that the initial WRA appointments for participants took longer to arrange the more the study progressed. We mitigated this as far as possible by employing independent WRAs as part of the study to provide cover when local authorities could not deliver services in their areas.
We lost 21% of participants through withdrawal or loss to follow-up, which was more than we anticipated from our pilot RCT.11 However, those lost from the study as a result of death constituted 4.8% of participants, fewer than the 5.6% who died during the 24 months’ follow-up in the pilot study.11 Those who left the study had poorer health than those who remained at 24 months. We were unable to interview anyone who dropped out of the study, so the reasons for attrition remain unclear.
An important limitation was the lower than anticipated proportion of participants in the intervention group (84/335, 22%) found to be eligible for additional benefits (and, similarly, after 24-month follow-up, in the control group). This had the consequence of significantly reducing the chance that we could detect an overall meaningful effect of the intervention, as any signal from the small number of those eligible was diluted in the intention-to-treat analyses. The relatively small numbers of new benefits recorded and the variation in the observed amounts resulted in substantial imprecision around point estimates for the value of benefits. For most of the financial benefits, owing to a lack of evidence, the economic analysis did not detect any significant differences between trial arms. However, CIs are wide and include economically important differences favouring either the intervention or the control group.
We designed the study to avoid contamination between trial arms. The participants were individually randomised, and those in the control group received no contact from a study WRA until after the 24-month follow-up. However, participants were free to seek welfare rights advice independently or to claim benefits independently during the course of the study. In data collected from the control group by interview at 24 months, a larger than anticipated proportion of participants reported new benefits that were not reported at baseline. When these were financial benefits, they must either have resulted from new claims or be the result of misreporting. When these were non-financial benefits (e.g. aids and adaptations in the home), it is possible that they were acquired by means other than welfare claims. Our qualitative work shed no further light on the source of these benefits (e.g. out of 20 control group participants interviewed, none indicated that participating in the trial had prompted them to seek welfare rights advice independently, yet 14 out of the 20 ultimately reported additional benefits at the 24-month follow-up), and the numbers and amounts of benefits reported, particularly non-financial, differed considerably between the 24-month interview and the CCS forms completed by WRAs at 24 months (see further below). Nevertheless, we are aware that, during the time of the study, a range of third-sector welfare rights advice service providers were operating in the North East, including Citizens Advice Bureaux, Age UK, Advice UK network, Law Centres Network, Shelter and the Money Advice Trust. Family and friends can also be important sources of advice on claiming benefits.
The main outcome (CASP-19) was assessed in interviews at 24 months, and by self-report using a postal questionnaire at 12 months. Such self-reported data may be subject to a variety of biases, in particular due to recall and social desirability. We found that the reports of benefits received at 24-month follow-up differed substantially between interview data and the data collected by WRAs in their CCS forms at 24 months. The reasons for this are unclear and, to ensure comparability with the intervention group, in particular in the economic evaluation, we decided to use the interviewer data. Sensitivity analyses were employed to explore the impact of data source. The discrepancy in self-reported data for additional non-financial benefits was substantial and could have altered the findings. However, comparing the reported numbers between groups suggested no significant effect of the intervention, although we cannot rule out the possibility that a meaningful difference existed. We were unable to obtain all of the CCS forms from the WRAs, resulting in some missing data on benefit outcomes in the control group at 24 months.
In our qualitative study, many participants referred to how benefits alleviated anxiety or worry. In our secondary outcomes measures, although we included the PHQ-9 depression scale, we did not include a specific measure of anxiety, and this is a limitation. We measured activities of daily living using the Townsend Activities of Daily Living scale, which was collected at baseline and at 12 and 24 months. This was included as a potential confounding factor in the outcome analyses. We decided that it would be inappropriate to use this scale as a secondary outcome because, although it reports on the ability to perform activities, it does not take into account whether or not, and from whom, help with activities is needed.
The costs in the control group were probably overestimated compared with those in the intervention group. For example, the durations for all other WRA activities that were not included in the cost analyses may have been higher in the intervention group. This is based on the assumption that, compared with usual practice, more claims for additional benefits may have been picked up by the WRA in participants’ homes, which would have increased the total duration of all activities in the intervention group.
Owing to the number of data collected by means of both participant questionnaires and the CCS that had to be analysed, the aim of the cost-effectiveness analyses was to use as much information as possible to provide an overview of which benefits (out of a potentially large range) were the most frequently awarded. Not all information (e.g. partner benefits and one-off payments from questionnaire data) were included in the final analyses, largely because there were missing duration data. However, as there was no evidence that the number of benefits reported in the questionnaires differed substantially between the trial arms, the results should not have been affected by this decision. Given that the information on durations was essential for the analysis, and was not collected for participants in the control group, estimates of the time a benefit was received in the control group were based on the estimates of the duration of benefits obtained for the intervention group. This may have limited the number of financial benefits considered and, therefore, may have led to an underestimate of the financial benefits in the control group. However, as the intervention was supposed to increase the number of benefits claimed, it was thought that this underestimation would be negligible.
Cross-validation between the CCS and questionnaire data for the intervention group was used to assess the validity of both data sources. This work showed that the number of newly awarded financial benefits recorded for the intervention group in the CCS was slightly higher than in the self-reported questionnaire data. Although a similar pattern of under-reporting may have occurred for those in the control group, the net impact on differences in value of benefits is likely to be small.
Finally, most likely as a result of the age range of the population and the trial period of 2 years, the number of participants lost to follow-up was relatively high, which was reflected, for example, by almost 23% of EQ-5D-3L data missing in each trial arm at the 24-month follow-up. There was also evidence that those remaining in the study at 24 months were healthier than those who dropped out for any reason.
Strengths and limitations in relation to previous studies
The trial was designed carefully to overcome the key methodological weaknesses of previous research. These included a lack of randomisation or controls; a limited range of outcomes without clear theoretical justification; limited statistical power; very short-term follow-up; a lack of economic evaluation; and a lack of process evaluation offering explanatory potential (see Chapter 1 for a detailed discussion of how these limitations were addressed).42,43
We optimised the intervention to maximise the likelihood of successful claims for those eligible by providing the intervention in people’s own homes, so as to avoid requiring those with health problems to travel;33 ensuring that there was active assistance with claims, so as to avoid the significant challenges that people can face in completing complicated claims forms;12,31,110 and providing training, information and guidance for both WRAs and GPs in assisting claims, so as to ensure that the welfare rights advice was delivered with maximal fidelity.11,12
We targeted the intervention to ensure that it was delivered most efficiently to those most likely to benefit from the intervention. We did this by identifying general practices in the poorest areas of the North East, using methods similar to those used in previous studies.72 However, we found that this did not guarantee that either the practices or the individual participants were similarly socioeconomically deprived (i.e. in the lower two-fifths of IMD distribution).
Our qualitative findings were remarkably similar to those identified in our pilot RCT,12 completed more than 10 years earlier. They demonstrated a range of potentially important impacts on HRQoL at an individual level, which we had anticipated might translate into detectable quantitative improvements in CASP-19 and secondary outcomes in this trial. The most notable difference from the pilot study to emerge reflected wider societal discourses on welfare entitlements, particularly the stigma and shame associated with claiming benefits.111 As has been found elsewhere, being viewed as an undeserving claimant is the key form of benefit stigma,112 and participants went to considerable lengths to justify the legitimacy of their claim by referring to their lifetime contributions into the welfare system. Professionals expressed a range of concerns about the impact of government austerity measures on welfare benefits and services, measures that were not present at the time of our pilot study and that are disproportionately impacting hardest on the poorest areas with the worst health outcomes.106,107 However, in the context of a rigorously conducted RCT, neither of these issues seems likely to have affected the outcome of the trial, as they would probably have affected both trial arms equally. That said, it is possible that changing views on benefit entitlement adversely affected older people’s willingness to participate in the trial, which may in turn have affected the response rate adversely. It was also evident during the study that the ability of welfare rights advice services to meet the study’s needs became more constrained over time.
Meaning of the study: possible mechanisms and implications for policy and practice
Altogether, the findings of this study do not provide sufficient evidence to support the commissioning of domiciliary welfare rights advice as a means of promoting health among older people. Nevertheless, taking into account the potential limitations of the study, we cannot rule out the possibility that the intervention had a potentially beneficial effect, and that this might be cost-effective. The findings in relation to the trial end points are somewhat surprising, given the qualitative findings, which suggest important impacts on HRQoL at an individual level. There are a number of possible explanations for this. First, the smaller than anticipated proportion of participants in the intervention arm eligible for new benefits will have considerably diluted the effect of the intervention on outcomes, resulting in an undetectable signal from the primary or secondary outcomes. Second, the receipt of additional benefits may take longer to convert into changes in HRQoL than we had time to measure. Third, we may have measured the wrong outcomes. Finally, there may be no measurable effect. Each of these explanations is now discussed further.
Our method of identifying suitable practices yielded ones that, despite being based in relatively poor areas (i.e. in the lower two-fifths of the IMD distribution), did not result in trial participants with equivalent levels of socioeconomic deprivation. This might have been because there were fewer such potential participants in practices than anticipated or because older people at the poorer end of the socioeconomic spectrum were not contactable or were less willing to participate. It is also possible that, when compared with the time our pilot trial was undertaken, there are now fewer older people entitled to unclaimed benefits. However, data collected nationally do not support this proposition. For example, around two-fifths of pensioner households entitled to Council Tax Benefit and one-third of those entitled to Pension Credit are still not claiming these benefits.35 It seems most likely that our recruitment method failed to identify and engage those most likely to be in need of the intervention. This has important implications for future evaluations and for service delivery models. More targeted approaches to identifying evaluation participants eligible for new benefits are warranted, as suggested by key stakeholders interviewed in our qualitative interviews.
We identified a correlation, albeit one that is relatively weak, between time since receipt of benefit and level of CASP-19 at 24 months in the intervention group. This, coupled with the lack of overall effect at 24 months, and the longer than anticipated time (median 58 days: substantially greater than the intended 14 days) taken by WRAs to conduct initial assessments of participants in the intervention group, suggests that a follow-up of longer than 24 months may have made it possible to detect a stronger effect. The feasibility of such a long-term follow-up (e.g. 36–60 months) in a new randomised trial may be problematic as, in our qualitative work with older people during the design of this trial, participants felt that it would not be acceptable for those in the control group to wait longer than 24 months for the intervention.1 Nevertheless, further follow-up of this trial cohort would be possible and may yield important new findings.
In developing this trial we focused considerable efforts on identifying the most appropriate outcomes. We based our decisions on existing literature as well as on the findings of our prior qualitative research.12,52 This work pointed us towards the likelihood that the receipt of additional benefits among those living in socioeconomically disadvantaged circumstances might have its greatest impact on HRQoL. The CASP-19 measure57,63 captured four domains (control, autonomy, self-realisation and pleasure) that most closely mapped onto the theoretical constructs defined in this prior research. Nevertheless, it is possible that this measure failed to capture sufficiently strongly the domain(s) of health or HRQoL that most closely accord with the impacts of increased resources on health. We also failed to detect any effect using a range of secondary outcome measures that we might have expected to demonstrate some change, such as measures of mental health, although our lack of an explicit measure for anxiety is a limitation previously acknowledged. The exact mechanisms of this relationship remain unknown.
It cannot be ruled out that the receipt of additional benefits failed to have any measurable effect on health or HRQoL. Although on first consideration this seems implausible, the context in which this impact is expected to occur needs to be taken into account. The participants in this trial were older people (aged ≥ 60 years), many of whom (particularly those who were more socioeconomically disadvantaged) were in relatively poor health, suffering a range of chronic, non-communicable conditions. These conditions may have resulted from a lifetime of exposure to unhealthy environments or behaviours, consequent on social disadvantage. The potential of these participants’ rate of decline to reduce might therefore be severely constrained by their conditions, such that the amounts of additional income or the advantages of non-financial benefits awarded were too little and too late to result in measurable impact.
Although it has proved all too easy to demonstrate strong socioeconomic patterning of health by measures of socioeconomic position in observational research,3,4 few studies have been able to show, under experimental conditions, that increasing access to resources results in better health.20 Although this may seem counterintuitive, it is important to remember that we do not yet have a clear understanding of the causal relationship between socioeconomic factors and health outcomes. Some progress has been made in the last 15–20 years, with research identifying some key pathways.32 This evidence suggests that the relationship is likely to have multiple pathways, some of which may be interdependent, leading to multiple outcomes. Studies such as the trial reported here may have simply not measured the right combination of exposures, outcomes or confounding factors to be able to pick up a measurable signal.
Nevertheless, in this trial we did identify some differences between the intervention and control groups at 24 months that offer tantalising signals that welfare rights advice may have an impact on health. The proportion benefiting from personal care in their home increased in the intervention group compared with controls, indicating that the intervention may have helped participants gain access to much-needed care, which could help them to maintain their independence and access to beneficial social relations. These findings were corroborated by the qualitative data, which provided ample evidence that the intervention led to valued outcomes among those who gained financial or non-financial benefits. Finally, there was weak evidence that the longer participants had benefited from additional financial or non-financial resources, the higher their CASP-19 scores were, an indication that impacts may have been developing over time.
If the intervention is effective, it is probably cost-effective. It proved remarkably cheap to deliver (£44 per case), even in comparison with the usual practice of welfare advice not being delivered in people’s own homes (an average additional cost of £17 per person). The estimated cost per QALY gained was £1914, well below the NICE threshold of £20,000, although with only a 60% chance that the actual cost per QALY was below this value.
Taking into account all of our findings, we remain equivocal about whether or not domiciliary welfare rights advice is effective as a health intervention as assessed in the context of this trial. It is possible that the intervention will yield positive impacts after a longer period of follow-up. It is also possible that important impacts will be identified in further evaluations that overcome the shortcomings of this research. Nevertheless, for those who receive unclaimed benefits as a result, the intervention remains important socially and economically and our research does not suggest that local government or third sector organisations should reduce their efforts in this area. Given that many of the unclaimed benefits for those aged ≥ 60 years are health-related, our research suggests that it will be of value to health care if professionals opportunistically identify and refer people to welfare rights advice services who they believe may be eligible for unclaimed benefits
Unanswered questions and future research
While much fundamental research is still needed to understand the causal pathways between socioeconomic position and health, a significant onus also remains on the research community to provide evidence to demonstrate whether or not improved socioeconomic circumstances result in better health. It would also be prudent to conduct further experimental studies to explore the impact of worsening socioeconomic circumstances on health, particularly in older people, as ecological study evidence suggests that important impacts of austerity measures could be mitigated by interventions such as welfare rights advice.113
It is unknown if a trial such as this could be replicated using the recruitment of a sample population of those in greater need (as assessed by eligibility) of welfare benefits. The challenges of achieving this are not inconsiderable. It would be important to identify participants on the basis of their own socioeconomic position rather than (or perhaps in addition to) using an ecological measure (e.g. IMD score associated with the general practice), as was used in this study. Recruitment and retention would probably be lower with such a population, and practical and analytical strategies would need to be adopted to minimise and mitigate the effects of the potential bias introduced.
Given the constraints on conducting this trial, it seems unlikely, on ethical grounds, that a similar but necessarily larger trial could be conducted using longer follow-up in order to see whether or not impacts of the intervention emerge over a period of > 2 years. However, it might be possible to conduct an alternative form of evaluation, perhaps taking advantage of a natural experiment in which a cohort of older people, some of whom have and some of whom have not claimed the benefits to which they are entitled, are followed up over an extended period. Such a study would need to make use of routine data to assess outcomes, and could explore the impact of differing lengths of time in receipt of benefits on outcomes. However, without targeted welfare rights advice providing a means to access for those currently not claiming their entitlements, such a study might suffer from similar problems, as sufficient claimants are needed in whom to measure an effect.
Future evaluations of welfare rights advice will need to consider carefully the outcome measures of interest. Taking into account the findings of recent research on psycho-neural pathways that show promise in explaining socioeconomic patterning of health outcomes,114,115 it may be possible to determine more proximal intermediate physiological outcomes, such as cortisol levels, which can be assessed non-invasively and might offer a more sensitive signal.
In the meantime, it may be of value to continue follow-up of this trial cohort to identify whether or not outcomes diverge among the intervention and control groups over a more extended time period (e.g. 2–5 years). The potential costs and burdens of such longer-term follow-up would need to be considered carefully, although follow-up using routine data (from primary care) focusing on independence and morbidity might offer a cost-effective and ethically uncontentious solution.