Randomised controlled trial with economic and process evaluations of domiciliary welfare rights advice for socioeconomically disadvantaged older people recruited via primary health care (the Do-Well study)

Article history

The research reported in this issue of the journal was funded by the PHR programme as project number 09/3009/02. The contractual start date was in December 2011. The final report began editorial review in April 2016 and was accepted for publication in October 2016. The authors have been wholly responsible for all data collection, analysis and interpretation, and for writing up their work. The PHR editors and production house have tried to ensure the accuracy of the authors’ report and would like to thank the reviewers for their constructive comments on the final report document. However, they do not accept liability for damages or losses arising from material published in this report.

Declared competing interests of authors

All authors received a grant of £28,000 from the North East Strategic Health Authority in 2012 to cover the costs of delivering the intervention, associated training and other non-research costs of this study. Elaine McColl has been a subpanel member of National Institute for Health Research (NIHR) Programme Grants for Applied Research and Programme Development Grants since June 2008. She was also an editor for the NIHR Journals Library Programme Grants for Applied Research programme from July 2013 to March 2016. Luke Vale has been a panel member of the NIHR Health Technology Assessment Clinical Trials Board since 2014, a panel member for NIHR Programme Grants for Applied Research from March 2008 to June 2016, and Director of the NIHR Research Design Service for the North East of England since April 2012. Martin White is a member of the NIHR Journals Library Editorial Board. He is Programme Director of the NIHR Public Health Research programme and Editor-in-Chief of the NIHR Public Health Research journal (he has held both roles since October 2014).

Dedication

We dedicate this report to Emma Noble, the lead researcher on this project, who died tragically, aged 46, in the second year of the study. Emma was a registered general nurse who worked in the NHS for 14 years prior to her appointment to Newcastle University in September 2004. Emma worked as a researcher in the School of Neurology, Neurobiology and Psychiatry, and the School of Education, Communication and Language Sciences, before she was appointed as a Research Associate in the Institute of Health & Society. Emma worked on the Do-Well study from its inception and was central to establishing the trial. She was a highly valued member of the team. Her sudden and unexpected death was a shock, not only to her family, friends and colleagues, but also to study participants to whom she was a great source of support. She is greatly missed.

Copyright statement

© Queen’s Printer and Controller of HMSO 2019. This work was produced by Haighton et al. under the terms of a commissioning contract issued by the Secretary of State for Health. This issue may be freely reproduced for the purposes of private research and study and extracts (or indeed, the full report) may be included in professional journals provided that suitable acknowledgement is made and the reproduction is not associated with any form of advertising. Applications for commercial reproduction should be addressed to: NIHR Journals Library, National Institute for Health Research, Evaluation, Trials and Studies Coordinating Centre, Alpha House, University of Southampton Science Park, Southampton SO16 7NS, UK.

2019 Queen’s Printer and Controller of HMSO

Socioeconomic inequalities in health among older people

A vast body of observational evidence on socioeconomic inequalities in health suggests a close relationship between access to resources and health status that is positive, progressive and has no apparent thresholds. 3,4 Health inequalities are universal across time, nations, societies and the human life course. Socioeconomic differences in health persist into old age, and socioeconomic inequalities in self-reported physical and mental health widen in early old age. 5,6 Individuals with mild cognitive impairment exhibit poorer financial and health literacy. 7 Low household wealth is strongly associated with poorer life satisfaction and quality of life. 8 The poorest older people have inadequate access to services essential to health and well-being. 9 Older people, especially those in poor health, therefore often need additional income and support to maintain their independence, including payments for care, domestic help and aids and adaptations to the home. 10–12

Resource-based interventions to promote health

Research into the differential provision of welfare across nations has shown that it can exert an influence on subjective well-being, morbidity and mortality. For example, older people are emotionally better off13 and at lower risk of suicide in welfare states more generous than the UK. 14 Almost half of the reduction in excess winter mortality since 1999/2000 has been attributed to winter fuel payments. 15 Key theories that explain how money influences health include materialist explanations (e.g. money buys health-promoting goods and the ability to engage in a social life in ways that enable people to be healthy, and enables the avoidance of health risks in the environment); psychosocial mechanisms (e.g. the stress of not having enough money may adversely affect health, and having adequate resources may relieve stress); behavioural factors (e.g. people living in disadvantaged circumstances may be more likely to have unhealthy behaviours); and being in poor health may affect education and employment opportunities in ways that affect subsequent health. 16

In theory, increasing individual or group access to material, social or financial resources (so-called ‘assets-based’ approaches)17 should result in improved health,4,18,19 yet little research has directly evaluated the impact of increasing resources on health. 20 Ecological studies following the reunification of Germany have suggested important impacts of increased income on mortality, although a range of other factors may have played a part. 21,22 A systematic review20 of 10 North American randomised controlled trials (RCTs) of income supplementation experiments targeting a range of age groups, carried out in the late 1960s and 1970s, showed that none had reliably assessed the effects of increased income on health. The authors pointed out that, although such experiments are unlikely to be repeated, one way of assessing the health impact of increasing financial resources on health would be to evaluate the impact of assisting claimants to obtain full welfare benefit entitlements. 20

Tackling health inequalities has become a major policy priority for the UK, highlighted, for example, in the White Paper on public health (Saving Lives: Our Healthier Nation). 23 Following publication of the Acheson report24 and the advent of Health Action Zones in the late 1990s,25 there was an increase in welfare rights advice projects linked to primary care in the UK. Welfare rights advice provision in primary health-care settings can reduce, by an estimated 15%, the time general practitioners (GPs) spend on benefits issues, and leads to fewer repeat appointments and fewer prescriptions. 26 In 1999, Reducing Health Inequalities: An Action Report27 highlighted welfare rights advice as a potentially effective intervention for reducing health inequalities. This proposal was endorsed by the UK government’s Marmot review in 2010. 3

Social welfare for older people and the underclaiming of entitlement

In the UK, a range of financial and non-financial welfare benefits is available; these benefits have different purposes and different criteria for entitlement. Some are means-tested (income-related) and others are dependent on an assessment of health or other needs. Means-tested benefits include income-replacement benefits (e.g. income-related pension credit, and income-related financial support with housing costs). Non-means-tested benefits are intended to help meet the additional needs of those with health or social care problems (e.g. meeting the extra costs associated with ill-health or disability, carer’s benefits to supplement/replace earnings for people who provide support or bereavement benefits for people whose legal partner dies). In addition to financial benefits, material support can be offered to those in need (e.g. mobility aids and housing adaptations, such as rails, ramps and bathroom aids). Financial and non-financial benefits are variously administered through the Department for Work and Pensions, local authorities, housing associations and charities. Welfare rights advisors (WRAs) in local authority social services departments and third-sector organisations (e.g. Citizens Advice Bureaux, Age UK and other charities) help by undertaking financial assessments, recommending whether or not a client might be eligible for a benefit and sometimes offering active assistance with completing claims. Active assistance may also involve liaising with health or social care professionals for evidence of diagnosis or care needs.

The non-claiming of welfare entitlements among older people is a long-standing problem, which is currently increasing. 28 A large proportion of eligible welfare benefits remains unclaimed,28 and many of these are health-related benefit entitlements of vulnerable groups, such as older people. 28,29 Failure to claim entitlements is associated with a number of factors including the complexity of the benefits system,30 lack of knowledge about entitlements and difficulty in making claims. 12,31–33 In recent British studies, the bureaucracy associated with applying and uncertainty regarding the outcome of any claim, the amount of the award, autonomy and independence were reasons cited by people who were entitled to but did not claim benefits. 12,31–34 In addition to the state pension, there are a number of means-tested and non-means-tested benefits that can be awarded to older people if entitlement conditions are fulfilled. The level of underclaiming varies depending on the benefit concerned, but it is estimated to be at least 33% for Pension Credit and 40% for Council Tax Benefit. 35 Entitlement to one benefit can often act as a ‘passport’ to others, as many of the benefits aimed at people over the state retirement age are linked together in a complex network of entitlements that is often difficult for people to access without expert assistance.

Welfare rights advice services and their evaluation

Our systematic review of the health, social and economic impacts of welfare rights advice services in health-care settings32 identified numerous studies that demonstrated the financial and material benefits of such services. Welfare rights advice provided by local authorities and third-sector organisations is known to increase the uptake of benefits among those eligible, particularly when this involves ‘active assistance’ with benefit claims. 24,36 Studies have also shown that the receipt of benefit entitlements can be increased by providing information and advice in general practice, particularly in relation to those benefits that are health related. 37–41 However, our systematic review identified only two studies that investigated the health impact of welfare rights advice,42–44 one of which found an improvement in health-related quality of life (HRQoL) in some of the subscales of the Short Form Health Survey-36 (SF-36). 42,43 However, both studies demonstrated the difficulties of identifying and measuring appropriate health outcome measures when assessing the health effects of welfare rights advice in primary care. Neither study used a randomised controlled design, and both suffered from significant methodological weaknesses that rendered them inconclusive. Both studies evaluated a model of welfare rights advice delivery that was based in primary care, required referral from practice staff and did not offer a domiciliary service or active assistance with claims. Qualitative studies exploring the impact of welfare rights advice on clients in primary care have identified a range of health-related outcomes that can potentially result from the receipt of welfare rights advice, including changes in the physical, behavioural and, in particular, psycho-social domains of health. 12,31–33

Since 2006, few studies have added substantively to this literature. Two papers updated analyses included in our systematic review but yielded no new conclusions. 45,46 A study in a hospice setting audited referrals for welfare rights advice and found inconsistency in referral practices and a heavy workload for WRAs, but valuable potential of such referrals in terms of benefit eligibility. 47 A study in a UK musculoskeletal clinic48 examined the use of the Health Assessment Questionnaire49 as a tool to identify patients’ eligibility for welfare benefits. Although the authors found relatively high levels of eligibility for new benefits among those identified, there are inconsistencies in the numbers in the paper that make it difficult to interpret. Nevertheless, it does identify a potential screening tool for use in health care that might be of value in the future. Another study from some of the authors of this report (Moffatt, Noble and White) examined the use of welfare rights advice among 1174 cancer patients, assessing the viability of a service linked to clinical teams using qualitative methods. 50 The service proved feasible, with exceptionally high levels of successful claims (96%) and median benefits returned (£70/patient). Patients and staff valued the service highly, and health outcome evaluation was felt to be warranted. Krska et al. 51 used a cohort study with qualitative interviews among 148 patients in primary care to evaluate a Citizens Advice Bureaux-delivered welfare rights advice service. 51 They reported a decrease in prescription of hypnotic/anxiolytic medications 6 months after referral for advice, compared with 6 months before, but their analysis was uncontrolled. Practitioners felt that the service benefited patients and reduced workloads.

We conducted a pilot RCT to prepare for the definitive RCT described here, evaluating the impact of a domiciliary welfare rights advice service offered to people aged ≥ 60 years identified via primary care in disadvantaged areas. 11,12,52 In this pilot trial, 58% of participants were awarded either financial (median gain £55/week), non-financial (e.g. aids and adaptations to the home) or both types of benefits,11 confirming the feasibility and success of the intervention from the point of view of accessing unclaimed benefits. It also provided vital information on the feasibility of such a trial, which has helped in planning the definitive RCT reported here. In reporting on the pilot trial we identified a number of key design and methodological issues that would need to be addressed in a definitive evaluation. These are discussed below.

Study design, level of randomisation, contamination and dilution

An appropriate trial design was required, preferably with both randomisation and concurrent controls. Individual-level randomisation was considered preferable to cluster randomisation (e.g. at general practice level), as it required a smaller sample size. The potential problem with individual-level allocation was that there could be ‘contamination’ between intervention and control participants in the same general practice. This was more likely to be the case when welfare rights advice was available from an open-access service delivered in the general practice. However, by using a WRA who only saw patients in their own homes, we found in our pilot RCT that contamination did not occur; no control participants reported independently seeking welfare rights advice during a follow-up period, albeit a period of only 6 months. 11

Equipoise and the control condition

A key consideration in designing the proposed trial was whether or not there was genuine equipoise. Welfare rights advice is known to increase access to financial and material resources for eligible clients. However, our systematic review of published and grey literature indicated that there was no conclusive evidence that welfare rights advice leads to positive or negative changes in health. 32 We discussed these findings with WRAs, with directors of adult social services, with a selection of GPs and with members of the public in our target age group. We found each of these groups to be in equipoise with regard to the proposed trial health outcomes. Having established this, we also carefully considered the issue of study design and the ideal and feasible control conditions.

We considered that, ideally, controls should be adults as similar as possible to intervention group participants, but should not receive welfare rights advice, nor claim or receive new benefits, during the period of outcome follow-up. In clinical trials, it is usual to withhold the intervention from the control group because the health benefits of the intervention are not proven (i.e. clinical equipoise exists). Although this is the case with regard to the health impacts of welfare rights advice, as indicated above there is adequate evidence that welfare rights advice leads to significant financial and material gains for a proportion of recipients. Thus, it was considered ethically problematic to identify that control group participants were eligible to receive additional financial benefits, but either to keep this information from them or to tell them of their eligibility but not give them advice or help with claims. To circumvent this dilemma, we proposed that control participants should not receive a welfare rights assessment until the end of the trial period (i.e. following final outcome measurement). The full intervention (i.e. a full benefit assessment and active assistance with claims until resolved) would then be offered.

We had concerns that the WRAs might feel tempted to offer benefits advice to control participants before the 2-year ‘wait period’ had elapsed. We planned to avoid this by not informing the WRAs of the names of control participants until a few weeks before their benefits assessment was due (i.e. 2 years after their baseline assessment). The study team would hold control participants’ names securely during this period.

The design would thus avoid unfairly raising expectations among control participants. It would also help to avoid the potential problem of contamination, which could have arisen if control participants independently sought welfare advice (leading to dilution of the outcome effect), although we did not propose attempting to prevent this as we found little evidence of it in our pilot RCT. The proposed control condition is, therefore, in effect a ‘wait-list’ control, whereby the control group waits to receive the intervention 24 months after the intervention group.

It is, of course, possible that some members of both the intervention and control groups will die during the proposed 24-month follow-up period, which we would expect in the course of any prospective study of this age group. In our pilot study, we recorded seven deaths (four in the intervention group and three in the control group) out of 105 after 24 months’ follow-up. 11

One of the reasons that such interventions to date have not been rigorously evaluated for health impacts is in part because such research has previously been deemed unethical by researchers considering undertaking such evaluations,53 on the grounds that one cannot withhold benefits to which people are entitled. The proposed design of this RCT is fair because, at present, this kind of intervention is not routinely available to primary care patients and is generally only available to those who seek such services or are referred to them by a health or social care professional (e.g. a hospital social worker); these options remain open to patients in this trial. When targeted services are available in primary care, they tend to be short term and ad hoc. If we find any general practices in participating local authority areas with access to such services, they will be excluded from this trial. Genuine uncertainty exists about the proposed health-related outcomes because participants will not be denied any entitlement that they would otherwise receive and, at the time of the study, the health impact of the proposed intervention remains unknown. 32 We have determined that the research team and key stakeholders from health and social services are in equipoise about the proposed health outcomes.

Pragmatic versus explanatory

In the proposed trial, we know that not all participants in the intervention group will be eligible for additional benefits, and that those who are will receive variable amounts of financial and non-financial benefits. Ideally, we wish to examine the health impact of receiving versus not receiving such benefits, as well as examine the potential for a gradient of effect (‘dose–response’ relationship) by the amount of benefit received. However, to do so will require a substantially larger sample size than that proposed. In practice, therefore, the receipt of welfare rights advice is the intervention we will be evaluating (rather than receipt of specific benefits), as ‘welfare rights advice’ is the service being delivered. The proposed trial is, therefore, a pragmatic (intention-to-treat) RCT of this ‘complex’ intervention. 54 Nevertheless, we will also assess the potential for exploratory subgroup analyses looking at differential effects by participant characteristics (such as age and sex), and receipt/non-receipt of and levels of any benefits received. We anticipate that the trial will therefore contribute both to answering the question of whether or not the welfare rights advice intervention is effective in improving health and to providing new evidence on the more fundamental question of whether or not increasing resources leads to better health. 4

Length of follow-up

To enable the accurate assessment of the health and social effects of welfare rights advice, an appropriate length of follow-up is required. Our previous work suggested that considerable time may elapse between the first advice session and the receipt of new financial or material benefits. Often this is between 3 and 6 months, but it can be longer if the case is not straightforward or if there is an appeal. For example, in our pilot RCT, 45% had received their entitlements by 3 months after their welfare assessment, 85% after 6 months, 95% after 9 months and 100% by 12 months. 11 Given such delays in receipt of benefits, as well as the fact that any financial benefits may not be spent immediately, it seemed unlikely that the benefits would have substantial impacts on health within the first 12 months. In our pilot, which was not adequately powered for substantive analyses, we found no suggestion of differences in health-related outcomes between the intervention and control groups after 6, 12 or 24 months (although in the pilot trial control participants did receive the intervention after 6 months). 11 Nevertheless, it seemed likely that the longer the delay between receipt of intervention and measurement of outcomes, the greater the chance of demonstrating a substantive effect on health.

To assess the acceptability of a range of delays in receiving the intervention among control group participants, we undertook an experiment in the context of a focus group discussion with a representative sample of low-income older people. To achieve this, simulations of the RCT randomisation procedures were undertaken. The first simulation concerned a typical drug trial, and participants were given sweets whose colour depended on whether they were randomised to the intervention or the control group. Then, randomisation for the proposed trial was simulated. The concept of equipoise, with regard to the health impacts of welfare rights advice, was explained. Next, each group member was given an envelope from which they found out whether they were in the control group or the intervention group. If in the intervention group, they were allocated various types of benefit (e.g. Attendance Allowance plus Council Tax Benefit plus Housing Benefit), and the monetary value of these was revealed to them. We then talked through the various possible time delays until the control group would also receive their welfare rights assessment and advice. The time delays used were 3, 6, 9, 12, 18, 24, 36 and 60 months. The initial response to the design was that it was unfair to those in the control group. However, when it was explained that (1) although such services exist, they are not routinely targeted at or delivered to all people aged ≥ 60 years but are only available on referral or demand, (2) the findings of this study could influence the development of such services, involving collaboration between health and social services, and (3) that a substantial ‘wait’ between intervention and control groups is needed to establish any differences in health outcome, the consensus of the group was that a delay of 24 months would be acceptable in the context of the proposed trial. We therefore opted for a wait-list design for the proposed RCT, with a 24-month follow-up period for the main outcome assessment, followed immediately by delivery of the full intervention to the control group.

Selection bias

In our pilot RCT, GPs wrote to random samples of people aged ≥ 60 years, inviting them to respond with an indication of their willingness to participate in the trial (i.e. to ‘opt in’). 11 Using this method, 36% initially agreed to participate, 14% declined to participate and 50% failed to respond. Low levels of positive response to an ‘opt-in’ approach carries a risk of participation bias. 55,56 In their work on evaluating the impact of welfare rights advice for the Department for Work and Pensions,57 Corden et al. 58 routinely use an ‘opt-out’ method of recruitment for similar populations. With the approval of the NHS Research Ethics Service (NRES), we proposed using this type of recruitment method in this trial; this should have reduced the potential recruitment bias associated with ‘opt-in’ recruitment methods and increased the efficiency of trial recruitment.

Choice of outcome measures

Previously reported studies of the health effects of welfare rights advice have restricted reported health outcomes to general measures of health or psycho-social functioning (such as the SF-3642,59), together with measurement of financial gains.

In our qualitative research among recipients of welfare rights advice,12,33 we identified a range of potential benefits of advice, including:

• health (improvements in anxiety, depression, insomnia; reductions in medication or consultation)

• health-related behaviours (health-promoting changes in smoking, diet, physical activity and alcohol consumption)

• social (improvements in family or other relationships, reduction of social isolation, increased ability to work, ability to care for relatives, etc.)

• financial (debt rescheduling and receipt of new benefits, e.g. Attendance Allowance, Disability Living Allowance, Disability Living Allowance mobility component, Invalid Care Allowance, Incapacity Benefit, Housing Benefit, Income Support)

• material (e.g. access to free prescriptions, Council Tax exemption, entitlement to respite care, Meals on Wheels, rehousing or home modifications).

The qualitative findings of our pilot study12,33 summarised these perceived benefits of the intervention in terms of:

• increased affordability of necessities

• increased capacity to manage unexpected future problems

• decreased stress related to financial worries

• increased independence, including ability to travel, shop, visit the GP, etc.

• increased ability to participate in family life and society.

These findings are corroborated by a recent evidence synthesis undertaken to develop a logic model for the health outcomes of welfare rights advice services. 19 The resultant logic model has been used as the basis for a realist evaluation of the health impact of Citizens Advice Bureaux services, for which a protocol has recently been published. 60

In addition to qualitative work with study participants in our pilot RCT, we collected proposed outcome measures and relevant potential confounding factors. 12 The pilot trial was not sufficiently powered for substantive analyses, but the feasibility of measurements was good, and well tolerated by older people. The main outcome measure we assessed was the SF-36 instrument, as used in several previous studies. 42,59,61,62 Although this had demonstrated some potential, albeit in uncontrolled or non-randomised studies (e.g. positive changes in the mental health and emotional role domains),59 we were concerned that its domains did not sufficiently encompass the substantially wider range of reported impacts of welfare rights advice identified in qualitative studies, including our own (see Welfare rights advice services and their evaluation). 12,33 We therefore sought an alternative HRQoL measure that might best encompass key domains, such as independence, social participation and mental health. There is no single, ideal outcome measure that captures all of these domains, but the CASP-19 (Control, Autonomy, Self-realisation and Pleasure) instrument,57,63 developed specifically with a view to measuring quality of life in older people, comes close and has been recommended by Corden et al. 58 as a composite measure of the impact of welfare rights advice. 57 It is a self-reported summative index, comprising 19 Likert scale items in four domains: control, autonomy, self-realisation and pleasure. 63 Its performance has been examined in several prospective studies, including the English Longitudinal Study of Ageing (ELSA). 64,65

Generalisability

Our pilot trial was undertaken in one social services district (Newcastle upon Tyne) and in four general practice populations. 11 However, we know, from other work and discussions locally, that service delivery in welfare rights advice varies from area to area, as do general practice populations. To enhance the potential generalisability of the results, the RCT was, therefore, undertaken across a range of geographical and local authority areas (including urban and rural) and general practices. It seemed possible, indeed likely, that the present welfare regime would change during the course of the trial. The proposed intervention was not dependent on any particular set of benefits and was adaptable to any new regime. This added to its future generalisability.

Target population

Although we recognised that isolated older people who are eligible for benefits may live in all areas, in order to maximise the efficiency (and impact) of welfare rights advice services provided through primary health care, this RCT focused on practice populations in socioeconomically disadvantaged areas. Eligibility for health-related benefits (and failure to claim) increases with age, particularly post retirement; although there are other key target groups, such as single parents, non-claimants most likely to be accessed through primary care are predominantly in older age groups. 33,66–68 This trial therefore focused on a predominantly post-retirement population (those aged ≥ 60 years), residing in areas of economic deprivation.

The North East has some of the poorest health outcomes in England, coupled with high levels of socioeconomic disadvantage. From the 19th century, the regional economy was based on heavy industries such as deep coal mining, shipbuilding and steel making. Since the 1970s and the demise of heavy industry, the area has suffered economic decline due, in particular, to the closure of shipbuilding, coal mines and other heavy manufacturing. The post-retirement population of interest in this trial were born in the pre-and post-Second World War years (from 1920 to 1950), and many would have worked in these industries, which are associated with industrial-related conditions such as musculoskeletal injuries and diseases of the lung.

Nature of the intervention

The intervention delivered in this trial was based on standard advice services of the type found across local authorities in England when this study was designed. Welfare rights advice is not a statutory service, and provision varies across all local authorities in England, Wales, Scotland and Northern Ireland. Conventionally, however, these services are available only on demand or by referral. Thus, for example, an older person admitted to hospital may be referred by a hospital social worker, doctor or nurse for benefits assessment prior to discharge. Only some services have undertaken the targeting of welfare rights advice at a population level. 32 Those that have done so have found that there is a significant level of underclaiming in the general population and, in particular, among older people. 29 The proposed intervention is, therefore, a modification of a standard welfare rights advice service to target proactively a particularly vulnerable population in which we anticipated there would be high levels of underclaiming (i.e. those aged ≥ 60 years in disadvantaged areas). The only reliable population registers in England at a local level are the primary care patient registration lists held by GPs, which were used to sample this target group selectively.

In our pilot RCT, we identified that effectiveness and efficiency (in terms of successful claims) could be maximised by making the service domiciliary, as a substantial proportion of those aged ≥ 60 years have limited mobility, and during assessments clients often need access to information they keep at home. 33 Domiciliary visits also proved more popular with clients. In addition, we found that WRAs need to provide ‘active assistance’ with claims, for example completing claim forms for clients, as being unable to complete the forms is a key barrier to people claiming. 12,31,32 Finally, GPs need to have appropriate awareness of welfare entitlements and, for health-related benefits in particular, an understanding of the medical criteria on which decisions are made, so that they can support reasonable claims effectively in medical assessments requested by the Benefits Agency. Good communication between GPs and WRAs is essential to facilitate this. In our pilot RCT, we delivered education and training on these issues to all GPs in participating practices,11,12 another feature that is included in the proposed definitive RCT.

Process evaluation

Process evaluation is an essential element of designing and testing complex interventions. Process evaluation is used to assess the fidelity and quality of implementation, clarify causal mechanisms and identify contextual factors associated with variation in outcomes. 54 When evaluating the impact of an intervention, the emphasis of process evaluation is on providing greater confidence in conclusions by assessing the quantity and quality of what was delivered, and assessing the generalisability of its findings by understanding the role of context. 69

To draw conclusions about what works, process evaluations aim to assess fidelity (whether or not the intervention was delivered as intended) and dose (the quantity of intervention implemented). Intervention fidelity relates to adherence to the content of the study protocol and the process of ensuring quality and consistency in intervention delivery to all study participants. 70,71 This includes ensuring a clear intervention model, developing an intervention protocol, selecting appropriate staff to deliver the intervention, ensuring adequate training in the implementation of the intervention and providing staff with ongoing supervision. 70 In complex interventions, fidelity is not a straightforward process. In pragmatic trials the standardisation of the intervention to the study protocol will promote internal validity, but limiting variation may affect generalisability. 54

In addition to what is delivered, process evaluation can investigate how the intervention is delivered. This can provide vital information about how the specific intervention might be replicated, as well as generalisable knowledge on how to implement other complex interventions. Issues considered may include training and support, communication and management structures, and how these structures interact with implementers’ attitudes and circumstances to shape the intervention. Process evaluations also investigate the reach of interventions (whether or not the intended audience comes into contact with the intervention, and how). 69

Exploring the mechanisms through which interventions bring about change is crucial to understanding both how the effects of the intervention occurred and how these effects might be replicated by similar future interventions. Process evaluations may test hypothesised causal pathways using quantitative data as well as using qualitative methods to better understand complex pathways or to identify unexpected mechanisms. Context includes anything external to the intervention that may act as a barrier to or facilitator of its implementation, or its effects. Implementation will often vary from one context to another, however; an intervention may have different effects in different contexts even if its implementation does not vary. Complex interventions work by introducing mechanisms that are sufficiently suited to their context to produce change, while causes of problems targeted by interventions may differ from one context to another. Understanding context is, therefore, critical in interpreting the findings of a specific evaluation and generalising beyond it. Even where an intervention itself is relatively simple, unlike welfare rights advice, its interaction with its context may still be highly complex. 69 In the proposed RCT, we collected both quantitative and qualitative data to assess the process of intervention delivery, allowing us to explore the reach, uptake, fidelity and quality of the intervention, as well as provide contextual information that may prove valuable in explaining the observed outcomes.

Objectives of the randomised controlled trial

The overall aim of the study was to evaluate the effects on health and well-being of a domiciliary welfare rights advice service for independently living, socioeconomically disadvantaged older people (aged ≥ 60 years), recruited from general (primary care) practices.

Trial design

A pragmatic, individually randomised, single-blinded (researchers), parallel-group, wait-list controlled trial of domiciliary welfare rights advice versus usual care, with embedded economic and quantitative and qualitative process evaluations (Figure 1).

FIGURE 1.

Overview of study design.

Setting

The trial took place in socioeconomically disadvantaged areas in the North East of England, which included urban, rural and semirural areas, with no previous access to welfare rights advice services targeted to primary care patients.

The study was planned to take place in 10 of the 12 local authority districts in the North East of England (Stockton, Darlington, Middlesbrough, County Durham, Sunderland, South Tyneside, North Tyneside, Newcastle, Northumberland and Gateshead). Social services departments in these local authorities had agreed in principle to provide domiciliary welfare rights advice services. The intention was to recruit two general practices per local authority district with the help of the Primary Care Research Network – Northern and Yorkshire (PCRN-NY). Lists of all general practices from the local authority districts were obtained from the PCRN-NY and ranked according to deprivation score using the 2010 English Index of Multiple Deprivation (IMD) calculated at middle-layer super output area (MSOA) level for practice premises (main surgery) postcodes, in accordance with the method of Griffin et al. 72 Deprivation covers a broad range of issues and refers to unmet needs caused by a lack of resources of all kinds, not just financial. The English Indices of Deprivation attempt to measure a broad concept of multiple deprivation, made up of several distinct dimensions, or domains, of deprivation. Super output areas are geographical units for the collection and publication of small area statistics. There are currently two layers of super output area: lower-layer super output areas (LSOAs) and MSOAs. LSOAs have an average of 1500 residents and 650 households. MSOAs have a minimum of 5000 residents and 2000 households, with an average population size of 7500, and fit within local authority boundaries. WRAs established whether or not any of the practices in the most socioeconomically deprived two-fifths of the IMD distribution had existing dedicated or targeted welfare rights advice services. Those practices in the lower two-fifths of the deprivation ranking distribution, without existing dedicated or targeted welfare rights advice services, were eligible for inclusion and were sent a letter by the PCRN-NY inviting them to participate (see Appendix 1), along with an information sheet describing the study (see Appendix 2) and an expression of interest form to return directly to the PCRN-NY.

The PCRN-NY provided the study team with a list of all eligible practices that had indicated a willingness to participate in research. If more than two general practices per local authority expressed willingness to participate in the research, the intent was to list the practices randomly and then contact them sequentially until two practices from each local authority district had agreed to participate in the trial. Fourteen eligible practices originally volunteered to participate in the research, representing only eight of the local authority areas for which we had secured the services of domiciliary WRAs. As we did not achieve our target of two general practices per local authority area immediately, we took two further courses of action: (1) we asked those practices that had originally volunteered if they would be willing to recruit additional patients (specifically, twice the number originally requested); and (2) we attempted to recruit further eligible practices through informal research networks across the North East of England. The latter strategy resulted in three further practices volunteering to participate from local authorities already involved in the study. However, it was also necessary to ask three general practices that had expressed willingness to do so, to recruit double the number of participants (Table 1). Owing to the problems with general practice recruitment, the welfare rights advice services in two local authorities that were willing to provide them were ultimately not required and the study took place in eight local authority districts.

Participants and recruitment

Participants were volunteer patients aged ≥ 60 years (one individual per household) who were not resident in a nursing home or in hospital, were not terminally ill (as assessed by their GP) and were fluent in written and spoken English.

The PCRN-NY and the Comprehensive Local Research Networks offered personnel and financial resources to participating general practices in the North East of England to identify and approach research study participants. Each participating practice was asked to generate a random sample of up to 300 people aged ≥ 60 years from their practice register. Practice staff scrutinised their list to identify any patients terminally ill or known to be resident in hospital or long-term care, who were excluded. Those who were assessed as not able to participate in the research due to poor mental or physical health, as assessed by their GP, were excluded from the study. Practice staff also checked to ensure that only one person per household had been selected for this list. If two people from the same address were found, one was selected by practice staff at random (by flipping a coin) to be retained and the other was removed from the sample list. Not all practices had sufficient patients registered to be able to generate a list of 300 people aged ≥ 60 years from their practice register; in these circumstances, they listed as many as possible.

This list of up to 300 names (of people believed to meet the eligibility criteria) per practice was randomly ordered and the first 100 patients on the list were sent a letter (see Appendix 3) and patient information sheet (see Appendix 4) signed by the senior GP partner on behalf of the practice, inviting them to participate in the trial. The figure of 100 patients was determined on the basis of the recruitment rate in the pilot study and anticipated to yield the required sample in an optimistic, best-case scenario. The letter on practice-headed paper explained that, unless the participant objected by returning the opt-out form (see Appendix 5) to the practice in the stamped addressed envelope within 2 weeks, their name and contact details would be passed to the research team, who would then contact them directly to discuss the trial further and seek informed consent.

After 2 weeks, the names, addresses and telephone numbers of those who had not opted out were passed to the research team. Research interviewers contacted these individuals by telephone to arrange, if acceptable, a face-to-face meeting at a mutually convenient time in the participant’s own home. At the initial appointment, research interviewers sought written informed consent (see Appendix 6) and then proceeded to collect baseline data.

We monitored recruitment continuously to assess whether or not and when further patients should be invited by each practice. When it became apparent that we would need to approach more than 100 patients to achieve our proposed sample size, practices were asked to write to additional patients from their original list of 300. In two cases, practices contacted all remaining patients aged ≥ 60 years. In these cases, the total number of patients invited was 387 and 330 (practices 1 and 12, respectively). In the three practices that had offered to recruit additional participants, recruitment numbers were doubled at each stage of the process.

Randomisation

Following written consent and baseline assessment, participants were randomised in a 1 : 1 ratio to intervention or control condition, stratified by practice. Research interviewers notified the project administrator after each baseline assessment that a new participant had been successfully recruited. The administrator held sequential allocation tables for each practice, independently generated from random numbers prior to recruitment [generated by a statistician (AB) using Stata version 12 software (StataCorp, College Station, TX, USA]. The administrator allocated all participants to the intervention or control group in the chronological sequence in which they were recruited and immediately sent each participant a standard letter (see Appendix 7) informing them of their group allocation. Only the project administrator had access to the allocation tables, and the allocation was thus concealed from the research team, data collectors and statisticians. The allocation was revealed to the participant and (in the case of intervention group participants) the relevant WRAs. The administrator immediately informed the appropriate local WRA team member of the contact details of each newly allocated intervention group participant and requested that they should be visited for a welfare assessment within 2 weeks. The WRAs were sent lists of control group participants to assess 24 months later, once follow-up had been completed.

Blinding

Research interviewers, who collected data from participants at baseline and 24 months, were not notified of the allocation status of participants to ensure that they remained blinded for the duration of the study.

Intervention

Here the intervention is described as designed and intended, according to Consolidated Standards of Reporting Trials (CONSORT) and Template for Intervention Description and Replication (TIDieR) guidelines. 73,74 In Chapter 3, variations of this intention are documented and the implications are identified. The rationale underpinning the intervention components was rehearsed in Chapter 1.

The domiciliary welfare rights advice service comprised face-to-face welfare rights advice consultations and active assistance with benefit claims, delivered in participants’ own homes and tailored to their individual needs by a qualified WRA employed by local authority departments, or their contracted services, in the North East of England. In one local authority, welfare rights advice services were contracted and delivered by a third-sector organisation. Following randomisation, intervention group participants were given an appointment in their own home with a WRA within 2 weeks, during which participants underwent a full benefit entitlement assessment involving assessment of financial, material and welfare status; assessment of previous benefit entitlement and claims; discussion of current entitlement and options for action, including new claims (financial and non-financial). Active assistance with benefit claims and other welfare issues was given, which included completion of benefit application forms on behalf of the participant. Complex claims or those referred for further assessment or tribunal were managed as per their usual practice by WRAs. It was anticipated that initial assessments would last up to 60 minutes. Participants were followed up at home or by telephone as required by WRAs until they no longer required assistance (cases are usually ‘closed’ once all claims and appeals have been concluded), which could take several months. 11

In area K, one local authority WRA provided the intervention from the start of the project until April 2013, when budget reviews restricted the availability of the WRA for the Do-Well study. A freelance WRA took over and completed the intervention in this area. In area G, the local authority WRA volunteered to provide the intervention for the Do-Well study but withdrew before recruitment began; therefore, a freelance WRA provided the intervention in this area. In area J, a local authority WRA provided the intervention at baseline but was unable to continue at 24 months (i.e. to deliver the intervention to control participants) because welfare rights posts had been lost and a new team had been formed that combined local welfare provision with supported housing. One WRA was retained by the local authority to deal with complex welfare cases but did not have the capacity to continue providing the intervention for the Do-Well study; therefore, a freelance WRA provided the intervention at the 24-month follow-up. In area L, three local authority WRAs provided the intervention throughout the study. In area M, the intervention was provided by paid staff from the Citizens Advice Bureau. In areas H and F, one local authority WRA within each area respectively provided the intervention for the duration of the study. In area E, two local authority WRAs provided the intervention for the duration for the study.

Intervention reach

Intervention reach was assessed as the proportion of those eligible to receive the intervention who actually received it. Causes of participants not receiving the intervention as intended (e.g. participants withdrawing, refusing or being lost to follow-up) and reasons given by participants (in interviews and questionnaires) were recorded when available. We also analysed the socioeconomic patterning of receipt of the intervention, and receipt of welfare benefits using IMD 201072 scores assigned at household level by matching postcode to IMD score at LSOA level.

Eligibility and receipt of welfare benefits was assessed, by type of benefit, as a proportion of those assessed by WRAs in the intervention group at baseline. This was also assessed in the control group at the 24-month follow-up.

At the outset, the intervention was primarily to be funded and provided by welfare rights advice services in the 10 participating local authority areas in the North East. However, a contingency fund of ≈£28,000 was also secured from the North East Strategic Health Authority in 2012, prior to the start of the study, to fund any excess intervention costs and the costs of any training for WRAs and GPs to ensure the effective delivery of this service with a high level of fidelity.

Training and quality control

To ensure consistent approaches to medical assessments related to relevant claims, each participating general practice was visited by a member of the research team and provided with an information pack and guidance on the completion of medical information on benefit application forms (see Appendix 8). This information was developed by the study team, with the help of a senior WRA who was involved in training and quality control in our pilot RCT, and a GP who was a member of the study team for the pilot RCT.

All participating WRAs were invited to attend information sharing events prior to intervention delivery to agree the intervention protocol, which specified the procedures for delivering welfare rights advice and the follow-up actions in a standardised manner. Intervention procedure checklists (see Appendix 9) were then given to all WRAs prior to the commencement of the study to ensure consistent delivery. Study staff closely monitored the progress of intervention delivery and maintained regular contact with all WRAs.

Fidelity assessment

We assessed the fidelity of the intervention in a number of ways. First, we asked WRAs to record the date and time of each initial welfare rights advice assessment, so we could assess whether or not these were delivered on time (within 2 weeks of the baseline study data collection). Second, we assessed whether or not initial welfare rights advice assessments were delivered as intended. This assessment was carried out, as unobtrusively as possible, by analysing audio-recordings of WRAs undertaking this aspect of intervention delivery with a small subsample of study participants. We aimed to analyse one initial welfare advice consultation per WRA (i.e. n = 19). Audio-recorded consultations were assessed by a senior WRA from a local authority not involved in the Do-Well study, selected for her extensive experience as a WRA, supervisor and welfare advice team manager. Each WRA was contacted shortly after the start of the study and asked to audio-record the next consultation undertaken with a consenting participant, and to record a brief commentary explaining the case and the actions recommended. We explained to WRAs that, as part of the research, we needed to understand how they interacted with clients and how outcomes were achieved. We avoided explicit reference to judgements about their practice, as this might have led to practice that was different from usual. Each participant was informed about the nature of the fidelity assessments, and written consent was obtained for audio-recording of the consultation. If a participant refused consent, the WRA was advised to ask the next participant they were due to visit for an initial assessment. The fidelity assessments took place between December 2012 and February 2013. Each consultation was analysed against a checklist of criteria developed by the study team (see Appendix 10). This checklist assessed the overall quality of the consultation, whether or not the correct assessment of needs had been made and that, if warranted, the correct benefits were applied for according to standard procedures. The senior WRA who listened to the recordings completed a confidentiality agreement prior to assessment, as it was felt not possible to fully anonymise the recordings. All data were held in accordance with the Data Protection Act 199875 and all sound files were individually password protected. After analysis of the fidelity assessment, all recorded files were destroyed. The research team was provided with a summary of each consultation based on assessment against the criteria of needs assessment, appropriate benefits applied for and a brief commentary on the justification for the outcomes achieved.

Comparator (wait-list control condition)

Participants randomised to the control group received ‘usual care’ (standard practice) from both health and welfare rights advice services after randomisation until they had completed their 24-month follow-up assessment. They were given no advice regarding welfare rights as a part of the study intervention during this period. However, they were free to seek welfare rights advice independently from their local authority or any third-sector provider at any time. Participants who sought independent advice remained in the trial and were analysed in the control arm on the intention-to-treat principle, and details of any advice and ensuing claims and outcomes were recorded at the 24-month follow-up assessment. Following the 24-month follow-up assessment, participants in the control arm received the intervention, as delivered to the intervention group (described above), including all follow-up visits by WRAs and assistance with claims and appeals over the following months, until all claims had been resolved.

The participants were informed during recruitment, via the patient information sheet (see Appendix 4), that we wanted to recruit 750 people into the study. They were told that one group of 375 people would be given an appointment with the welfare advice service straight away and another group of 375 people would be given an appointment around 24 months later. Potential participants learned that the group they would be put in would be decided by chance, like tossing a coin, but that everyone would receive an appointment within 24 months. Once individuals agreed to participate in the study and completed baseline assessment, they were sent a letter (see Appendix 7) detailing which group they had been assigned to. Wait-list control participants were told that the group they had been assigned to would mean that they would see a WRA approximately 24 months after they entered the study.

Both intervention and control group participants remained clients of the welfare advice service beyond the end of the trial, if necessary, until such time as their help was no longer needed, as per usual welfare rights advice service protocols.

Data collection

Harms

At the outset, we were not aware of any major risks or harms associated with the delivery of the intervention. However, it was possible that older people could spend additional resources in ways that would be potentially harmful. These might include spending additional financial resources on alcohol or tobacco (with known risks of chronic diseases), ‘luxury’ foods, high in fat and sugar (e.g. chocolate), or gambling, which can be addictive and financially ruinous. It was also possible that the increased independence and mobility (which we hypothesised would be associated with access to additional resources) could result in greater environmental exposures outside the home, resulting in infectious diseases or accidental injury. Furthermore, the intervention could lead to greater use of car travel, resulting in lower levels of physical activity. It was also possible that older people would feel obliged to share any additional income with family members, who may be equally socioeconomically disadvantaged, thus negating the beneficial impacts on themselves. Older people may also be more vulnerable to external pressures, such as cold-calling from salespeople. We assessed potential adverse outcomes by (1) identifying negative (unhealthy) changes in all primary and secondary outcome measures; and (2) including additional, semistructured open questions in follow-up questionnaires and interviews on other, potential, unanticipated outcomes in order to document these and develop explanations.

Other quantitative data collected

Demographic variables were collected to characterise the trial participants and adjust for potential confounding in analyses, including age, sex, ethnicity, educational level attained, employment status and living arrangements (number of household members, paying for accommodation, and whether or not emotional support was available). In addition, two scales were used.

Functional ability was measured by the modified Townsend Activities of Daily Living scale,85 which assesses a person’s ability to perform eight activities. The possible range of scores is 0–16, with higher values indicating a greater ability to perform activities of daily living.

Life events score was measured by recording eight potentially serious events, including bereavement and significant illness, that might have occurred in the past 7 months, as well as their impact on the individual. 86

Sample size

A minimum of 318 participants needed to be followed up in each of the intervention and control arms (a total of 636) to provide 90% power at 5% significance level to detect a 1.5-unit difference in mean CASP-19 score57,63 at 24 months between the intervention and control groups, assuming a standard deviation (SD) of 8.7 and a correlation between baseline and 24 months of 0.74. The estimates of SD and correlation coefficients came from the results of ELSA (wave 4) restricting the analyses to those aged ≥ 60 years. 87 Estimating an attrition rate between baseline and 24-month follow-up of 15% (as experienced in our pilot RCT),11 we needed to recruit 750 participants to the study (375 to each group).

There has been no published work to establish a meaningful or clinically important difference on the CASP-19 scale. However, we based the above acceptable difference on data from waves 1 and 2 of the ELSA in those aged ≥ 60 years. We investigated the adjusted mean difference in CASP-19 at wave 2 between groups whose social or health circumstances had changed. 64 Examples of changes in CASP-19 score associated with changes in health or social circumstances that we might have expected to see in the proposed trial included ‘developed limiting illness’, –2.8 units; ‘developed depression’, –2.7 units; ‘lost access to car’, –1.8 units; and ‘increased chance will not meet financial needs’, –1.1 units. These differences on the CASP-19 scale suggest that a difference of 1.5 units would represent a minimally clinically important difference. 65 The chosen sample size also provided power to demonstrate some clinically significant differences in secondary outcomes. For example, 750 participants would provide 90% power to detect a difference between a prevalence of 11% and 4% of clinically significant depressive symptoms (PHQ-9 score of ≥ 10).

Data handling, record keeping and sharing

Baseline and 24-month data were entered directly during interviews, via a tablet computer, into a secure custom-built database for processing and management using a bespoke content management system on Microsoft SQL^® Server and ASP.NET (Microsoft Corporation, Redmond, WA, USA). A record was maintained of any changes made to the data post entry. All personal information obtained for the study was held securely at Newcastle University and was treated as strictly confidential. The project administrators undertook entry and verification of data from 12-month posted self-completion questionnaires into a Microsoft Excel^® (Microsoft Corporation, Redmond, WA, USA) spreadsheet, with a 10% random sample checked for data entry accuracy. The data collection and transfer in this study complied with NRES88 and Caldicott guidelines89 and the Data Protection Act 1998. 75

All patients were allocated a unique study identifier, which was used on all data collection forms and questionnaires to preserve confidentiality; names or addresses did not appear on completed questionnaires or on other data collection forms. Only a limited number of members of the research team were able to link the unique identifier to patient-identifiable details (name, address and telephone number) that were held on a password-protected Microsoft Access^® (Microsoft Corporation, Redmond, WA, USA) database. All study documentation was held in secure offices that were not open to the public, and all members of the research team with access to identifiable or anonymised data operated to a signed code of confidentiality. Transmission of original or hard copy records (e.g. questionnaires, interview recordings) was by secure fax, post or hand delivery by members of the research team or by the WRAs. Participants were informed in the patient information sheet (see Appendix 4) about the transfer of information to the research team and about levels of access to patient identifiable data, and were asked to consent to this.

At the end of the study, original questionnaires, interview transcripts, consent forms and final versions of all data sets will be securely archived in the Institute for Health & Society for 5 years following publication of the last paper or report from the study, in line with sponsor policy and Newcastle Clinical Trials Unit standard operating procedures. This also allows any queries or concerns about the data, conduct or conclusions of the study to be resolved. Anonymised data will subsequently be securely archived and made available for secondary analysis as appropriate. Details of data sharing arrangements are available from the corresponding author.

Trial data analysis

In this section, the methods used to organise and analyse the data are described. This is divided into three sections, covering the quantitative study, economic evaluation and qualitative analysis.

Qualitative study

Economic evaluation

The relative efficiency of the domiciliary welfare rights advice intervention was assessed in within-trial cost–consequences and cost–utility analyses using data collected during the 24 months of the trial follow-up. For the cost–consequences analysis, the costs and consequences of the intervention are reported separately. The cost–utility analysis combined cost data and HRQoL measures to estimate the incremental cost per quality-adjusted life-year (QALY) gained.

Estimates of cost took the perspectives of the public sector services (for the service delivery costs of the Do-Well intervention) and the Treasury (for additional benefits awarded). Sensitivity analyses were performed to assess the impact of different data sources and varying key assumptions and parameters on the cost-effectiveness of the intervention.

Ethics arrangements, governance and sponsor

A favourable ethics opinion was received from the UK NRES Committee South West – Exeter (reference number 11/SW/0260). The trial was registered as Current Controlled Trials ISRCTN37380518. The sponsor of the research was NHS North of Tyne.

Changes to protocol

In October 2011 (protocol 1–2), the protocol, participant information sheet and informed consent form were amended to include the possibility of long-term follow-up. In the event of an inconclusive outcome to the study at 24-month follow-up, it would be desirable to follow up participants at a later time point. Therefore, we amended the protocol to seek, at baseline, participants’ consent to contact them again at a later date. It was recognised that long-term follow-up would require further funding and a new protocol.

In May 2013 (protocol 2–3), the protocol was amended to correct some typographical errors. In addition, the covering letters designed to be sent out with the 12-month follow-up questionnaire (cover letter, reminder letter 1 and reminder letter 2) were added.

In August 2013 (protocol 3–3.1) the protocol was amended to increase the number of participants able to take part in the qualitative element of the study from 30 trial participants and 10 professional participants, to up to 70 trial participants and up to 20 professional participants, subject to data saturation.

In February 2014 (protocol 3–4), the protocol was amended to allow us to include other household members in our qualitative interviews. This involved the production of a separate participant information sheet and consent form for other household members (see Appendices 15 and 16).

Protocol version 4, our final approved version, is available at www.nets.nihr.ac.uk/projects/phr/09300902. 103

Independent Trial Steering Committee

An independent TSC provided overall supervision of the trial. The independent TSC comprised Professor Stephen Walters (chairperson), Professor of Medical Statistics and Clinical Trials, School of Health and Related Research (ScHaRR), University of Sheffield; Professor Colin Green (deputy chairperson), Professor in Health Economics and Head of Health Economics Group, Peninsula College of Medicine and Dentistry, University of Exeter; Mr Nick Whitton, Head of Commissioning for Adult Services, Adult and Community Services, Durham County Council; Mrs Sally West, Strategy Adviser – Income and Poverty; Age UK; Dr Anne Corden, Senior Research Fellow, Social Policy Research Unit, University of York; Christine Smith (lay member); John Marshall (lay member); Professor Martin White (Chief Investigator); the study statistician (Ms Denise Howel); and the study project manager (Dr Catherine Haighton). Observers from the National Institute for Health Research Public Health Research programme and our sponsor were invited to all independent TSC meetings. Following the initial pre-study meeting, the independent TSC met annually. Its role was to monitor progress and supervise the trial to ensure that it was conducted to high standards in accordance with the protocol, the principles of good clinical practice, relevant regulations and guidelines, and with regard to participant safety and well-being. A written charter was agreed and used by the independent TSC (see Appendix 19).

Data Monitoring and Ethics Committee

This was a low-risk trial and major safety data were not anticipated; therefore, a Data Monitoring and Ethics Committee was not convened.

Patient and public involvement

We engaged with service users from the outset and throughout the study. The research design was discussed with a representative sample of low-income older people to assess its acceptability. We undertook a simulation experiment in the context of a focus group discussion with a representative sample of low-income older people (discussed in detail earlier, see Length of follow-up). These members of the public provided valuable insight and advice regarding the study design and patient-relevant end points at the outline stage. Throughout the study, direct patient involvement, via a number of focus groups with Age UK members, also supported the development of suitable letters of invitation to participate, participant information sheets and covering letters explaining the study instruments. There were also two lay members of the TSC (Christine Smith and John Marshall), who provided valuable input throughout the course of the study.

Process evaluation

In this section, measures of the implementation of the trial and the intervention will be presented.

Trial implementation

Figure 2 shows the recruitment and flow of participants through the trial, using the CONSORT format. 73 Nearly 4000 primary care patients aged ≥ 60 years were initially approached by 17 general practices. The recruited participants were spread over the 17 general practices, as shown in Table 5. These practices were chosen to be in the lower two-fifths of the deprivation ranking distribution. The average deprivation level of the 17 participating practices (based on the IMD score at the MSOA level for practice postcode) was lower than that among the remaining 363 practices in the North East [IMD score at MSOA level: 27.0 (SD 10.4) vs. 38.5 (SD 11.5)].

FIGURE 2.

The CONSORT flow chart of participants in the Do-Well RCT. WR, welfare rights. Reproduced from Howel et al. 2 This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution International license (CC BY 4.0), which permits others to distribute, remix, adapt and build upon this work, for commercial use, provided the original work is properly cited. See: http://creativecommons.org/licenses/by/4.0/.

Reproduced from Howel et al. 2 This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution International license (CC BY 4.0), which permits others to distribute, remix, adapt and build upon this work, for commercial use, provided the original work is properly cited. See: http://creativecommons.org/licenses/by/4.0/.

TABLE 5 - Number recruited (%) to trial by general practice

Practice code	Mailed (n)	Responders (n)	Recruitment rate (%)
1	387	52	13.4
2	295	61	20.7
3	200	44	22.0
4	200	51	25.5
5	300	73	24.3
6	100	25	25.0
7	100	17	17.0
8	100	26	26.0
9	300	47	15.7
10	300	70	23.3
11	200	35	17.5
12	330	75	22.7
13	300	54	18.0
14	200	31	15.5
15	200	30	15.0
16	200	47	23.5
17	200	17	8.5
Total	3912	755	19.3

Of those patients approached, 1770 (45%) opted out of further involvement by returning the invitation slip to their general practice. GPs sent the remaining 2142 names (55% of those approached) and their contact details to the research team. The chief investigator wrote to all of these patients inviting them to participate in the research. Of the 2142 invited, 825 (39%) declined to participate further at that stage, 405 (19%) were not contactable, 116 (5%) initially did not refuse but later declined to participate and 41 (2%) were not contacted as the recruitment target had been reached before they were needed. Those remaining were 755 primary care patients aged ≥ 60 years from participating general practices in socially deprived areas of North East England, all of whom agreed to participate, provided informed consent and were randomised to either the intervention or the control group. The participants were recruited between 11 May 2012 and 28 February 2013.

However, those who agreed to participate (n = 755) were, on average, less socioeconomically disadvantaged [IMD score at LSOA level: 29.0 (SD 16.0)] than non-participants [n = 1387; IMD score: 33.5 (SD 17.9)], and were more likely to be female (53.5% vs. 50.5%).

During the trial, 121 participants withdrew from the study, 36 were lost to follow-up and 36 participants died (see Figure 2 for details). The losses were balanced across allocation groups. In total, 562 participants completed the 24-month follow-up (intervention group, n = 283; control group, n = 279) and were available for analysis.

Receipt of intervention (reach)

As shown in Figure 2, 381 trial participants (50%) were randomly allocated to receive the intervention. The intervention group participants were offered welfare rights advice shortly after recruitment: Figure 3a shows the distribution of the time, in days, between randomisation and the first visit by the WRA, while Figure 3b shows the distribution of time between randomisation and closing the welfare rights advice case, which occasionally took > 12 months. The number seen (as intended) within 2 weeks by their WRA was 5 (1.5%) and within 4 weeks was 37 (11%). The median number of days from study entry to first WRA visit was 58 days (IQR 40–89 days) and the range was 0–403 days. The length of time taken for WRAs to see intervention group participants for their initial assessment increased over time.

FIGURE 3.

Distribution of (a) time (days) between randomisation and first WRA visit; and (b) time (days) from randomisation to welfare rights advice case being closed.

Table 6 shows whether or not the advice was received or if benefits were awarded among the 381 participants in the intervention arm. Of these participants, 335 (88%) actually received the intervention as intended. For those randomised to but not receiving the intervention (n = 46, 12%), the most commonly cited reason for not receiving was that the participant declined the welfare rights advice consultation (n = 23); this represented 6% of all who were eligible and 50% of those not receiving the intervention (in the intervention group). In addition, some participants completely withdrew from the study before intervention delivery (n = 16), while a small number of participants could not be contacted in order to arrange the welfare rights advice appointment (n = 7).

TABLE 6 - Welfare rights advice receipt and outcomes at 24 months for those in intervention arm (n = 381)

Includes declined welfare rights advice, and not awarded responses.

Includes withdrawn, unknown and non-contactable responses.

	Number (%)
Welfare rights advice received
Yes	335 (88)
No	46 (12)
Benefits from welfare rights advice
Yes	84 (22)
Eligible but refused	17 (4.5)
Noa	250 (65.8)
Awaiting outcome	1 (0.3)
Withdrawnb	29 (7.5)

In total, 84 of the 381 participants (22%) in the intervention arm were awarded an additional benefit, but this rises to 25% when expressed as a percentage of the 335 who received welfare rights advice. Table 7 shows the distribution of the benefits received for those who took up the offer of welfare rights advice. This information came from the records kept by the WRAs (CCS). There were some discrepancies observed between WRA records and those obtained when participants were interviewed at 24 months concerning new benefits that had been awarded. This is explored further in Chapter 5.

TABLE 7 - Distribution of benefits received by 24 months for the 335 participants receiving welfare rights advice in the intervention arm

Non-means tested is not-applicable to non-financial benefits.

Note

Reproduced from Howel et al. 2 This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution International license (CC BY 4.0), which permits others to distribute, remix, adapt and build upon this work, for commercial use, provided the original work is properly cited. See: http://creativecommons.org/licenses/by/4.0/.

	Number (%)
Type of benefit
None	250 (74.6)
Financial	65 (19.4)
Non-financial (aids and adaptations)	14 (4.2)
Both financial and non-financial	5 (1.5)
Not known	1 (0.3)
Of 84 participants who received benefits
Means- or non-means-tested benefits
Means tested	16 (19.0)
Non-means tested	49 (58.0)
Both means and non-means tested	19 (23.0)
Combination of type of benefit and means or non-means tested
Financial (means tested)	16 (19.0)
Financial (non-means tested)	34 (40.0)
Both financial (means and non-means tested)	15 (18.0)
Aids and adaptations (non-means tested)	14 (16.5)
Both financial and aids and adaptations (non-means tested)a	2 (2.5)
Both financial and aids and adaptations (means and non-means tested)	3 (3.5)

Table 7 shows that non-means-tested benefits were most commonly received. There were small numbers in each of the categories of different combinations of financial and non-financial benefits received. A detailed description of exactly which financial and non-financial benefits were received is given in Chapter 5.

Baseline characteristics of trial participants

To illustrate how representative the Do-Well participants were of other residents of England, Table 8 compares the demographic characteristics of the Do-Well participants with those of members of the ELSA cohort in wave 4 who were aged ≥ 60 years. The Do-Well trial participants were recruited from practices in the lower two-fifths of the deprivation ranking distribution in areas of the North East, whereas the ELSA cohort was recruited from the whole population of England. There were clear differences between cohorts on only a couple of variables: higher proportions of Do-Well participants lived alone and ‘were paying rent or mortgage’ (as opposed to owning their own home or, occasionally, living rent free).

Tables 9 and 10 show the baseline characteristics of the 755 participants for categorical and numerical outcomes, respectively, by trial arm. The distributions were well balanced between the intervention and control arms. Roughly half of the participants were male, living alone and not paying for accommodation. They were predominantly white, were educated to secondary school level, were retired, were never or ex-smokers and had a satisfactory level of emotional support. The average age was 70 years, while typical Townsend Activities of Daily Living scales were relatively high and stressful life events scores were relatively low.

Table 11 shows the distribution of the primary and secondary outcomes at baseline. The participants had typical values towards the more favourable end of each scale for quality of life, affordability index, standard of living, depression and healthy diet; and towards the less favourable end of the scale for social interaction and physical activity (PASE). The distributions were well balanced between the intervention and control arms.

Table 12 shows the baseline characteristics of the 755 participants for categorical and numerical outcomes for responders and non-responders at 24 months. Those who dropped out of the trial before the 24-month assessment on average tended to be a little older, slightly more likely to be male and have a lower average CASP-19 score at baseline.

Outcome analysis

Exploratory analyses

A set of exploratory analyses on those in the intervention arm investigated whether the primary outcome (CASP-19) at 24-month follow-up varied between those in subgroups defined by welfare rights advice received or benefits awarded. These subgroups were not likely to be balanced on key covariates, because socioeconomic and health-related variables are key eligibility criteria considered when a welfare award is made. Table 16 shows the distribution of sociodemographic variables for those who did and did not receive any welfare benefits: there were no great differences, but those awarded welfare benefits tended to be slightly older and more likely to live alone and be female, and less likely to be well educated and be able to carry out activities of daily living: there was little difference in mean IMD scores, which might have been expected.

Table 17 shows that there was little difference in the crude mean total CASP-19 score at 24-month follow-up between those in the intervention group who did and those who did not receive welfare rights advice, with a small unadjusted difference in means favouring those not receiving welfare rights advice (42.8 for those who received welfare rights advice vs. 44.2 for those who did not). However, after adjustment for key covariates (see Table 17), the direction of difference did not change, but this was not statistically significant (adjusted difference –2.1, 95% CI –5.5 to 1.3).

When comparing the subgroups who did and did not receive benefits (as opposed to advice), the lower part of Table 17 shows that there was a lower average CASP-19 score at the 24-month follow-up in those receiving benefits, for both total score and subscales (mean total score 39.2 for those who received benefits vs. 43.8 for those who did not). This might be explained by the fact that those who received benefits tended to be worse off at baseline, in terms of health and socioeconomic variables, than those who did not receive welfare benefits, and this could be reflected in the CASP-19 scores. After adjusting for these covariates, the difference in mean total CASP-19 score was smaller (adjusted difference –0.7, 95% CI –2.8 to 1.4), and there was no indication of a statistically significant or clinically important improvement in average CASP-19 in those receiving welfare benefits.

Secondary outcomes were also compared between those who did and those who did not receive welfare rights advice. Table 18 shows that the adjusted differences in mean between the two subgroups were all small with narrow CIs.

A comparison of secondary outcomes between those who did and those who did not receive any benefits was also undertaken. Table 19 shows that the adjusted differences in means between the two subgroups were all small with narrow 95% CIs, except for the physical activity score (PASE). The adjusted mean PASE score was significantly higher in those who were not awarded any benefits (adjusted difference –13.9, 95% CI –27.0 to –0.9); this may reflect the better health of those who did not receive welfare benefits, rather than any effect of non-receipt of welfare benefits on the ability or choice to exercise more.

A final comparison was between the CASP-19 scores at 24 months for those in the intervention arm who had been awarded a financial welfare benefit and those in the control arm who were later awarded a financial benefit (after 24-month follow-up). As they were all eligible for financial welfare benefits, these participants should be similar in their socioeconomic and health profiles. The 55 in the intervention group who had been awarded financial benefits had a mean CASP-19 score of 39.2 (SD 9.1), whereas the 48 in the control group (who were later found to be eligible) had a mean CASP-19 score of 39.7 (SD 9.4). After adjustment for covariates, the mean CASP-19 score was 1.4 higher in the control group (95% CI –2.0 to 4.7). This comparison shows again that there was little or no evidence that CASP-19 varied between a subgroup who had received benefits and a subgroup who had not.

A further exploration of any association between CASP-19 and receipt of welfare benefits in the intervention group was to look at the weekly amount of financial benefits (in pounds sterling). Figure 4 shows the association between these two variables; it can be seen that there is no indication that CASP-19 at 24 months is higher for those receiving greater financial benefits. However, this does not adjust for the covariates used in previous regression models. When adjustment was made for these, the regression coefficient for CASP-19 on weekly amount was 0.02 (95% CI –0.08 to 0.04) also showing a lack of association.

FIGURE 4.

Association between CASP-19 score at 24 months and weekly amount of financial benefit awarded.

The final exploration looked at the association between the length of time that a person had been receiving additional benefits and the CASP-19 scores at 24 months (Figure 5). It might be expected that among those who had only started receiving welfare benefits shortly before the assessment at 24 months, health may have improved less, and this might be reflected in a smaller change in CASP-19 score. However, the vast majority of people had been receiving benefits for at least a year by the time of final assessment. The correlation between the two variables was 0.39 (95% CI 0.16 to 0.58), a weak positive association.

FIGURE 5.

Association between length of time that participants were in receipt of additional benefits and CASP-19 score at 24-month follow-up.

Introduction

This chapter presents the findings of the qualitative study embedded within the RCT. We begin by presenting the sociodemographic characteristics of the qualitative study participants, including household members of trial participants, and professionals (see Tables 20–22). We then present findings on the acceptability of the research design and intervention, followed by those on the impact of the domiciliary welfare rights advice service, as experienced by trial participants and professionals. We then focus on the mechanisms of action and unanticipated consequences of the intervention, before finally examining the impact of external factors, such as cuts to the public sector, on this type of service and its delivery.

The findings are organised around the key themes identified during interviews and are presented for both trial and professional participants. Our presentation of the findings is interspersed with verbatim quotes to illustrate particular points, pseudonyms are used throughout, and any identifying information (e.g. place names) has been removed to preserve anonymity. The participants were made aware that their comments may be used in publications, and informed consent for this was obtained.

Participant characteristics

Tables 20 and 21 present social, demographic and welfare benefit outcome data for the 50 participants in the embedded qualitative study, 30 intervention (see Table 20) and 20 control (see Table 21), all of whom received the intervention as planned. Eight partners were also interviewed alongside trial participants, as indicated in Tables 20 and 21. Thirty-one women and 19 men took part, with six female partners and five male partners also interviewed. The age of the trial participant at the time of the interview is given. The average age was 72 years, ranging from 61 to 86 years. Most of the interviewees were living alone (widowed, n = 19; divorced/separated, n = 8; single, n = 4), with 19 living as part of a couple. Trial participants came from throughout the North East region and from urban, rural and semirural areas; the IMD scores ranged from 7.43 (least deprived) to 71.74 (most deprived). The trial participants were interviewed after receiving a welfare rights intervention and, for those in receipt of a financial or non-financial award, the interview took place after the award was received. The control group trial participants took part in qualitative interviews after their 24-month wait, and following intervention receipt.

Table 22 presents information about the 17 professional participants in the study. Thirteen women and four men were interviewed from the following sectors: welfare rights, public health, primary care and the civil service. Among the 10 interviewees from the welfare rights sector, four delivered the intervention in the trial, while the remaining six had management or strategic roles within that sector.

Acceptability of research design and intervention

Impact of the intervention

This section focuses on the impact of the intervention on financial status, health and well-being from the perspectives of trial participants and professional interviewees.

Mechanisms of action

Unanticipated consequences of the intervention

As we have demonstrated, many trial participants were highly satisfied with the intervention, its delivery and its outcomes. Trial participants did not highlight any adverse outcomes, harms or risks associated with the delivery of the intervention. Trial participants did not discuss spending their additional benefit income on potentially anticipated harms such as alcohol, tobacco, ‘luxury’ foods or gambling but rather used it primarily to afford basic household, transport and care costs. Furthermore, trial participants did not associate the independence and mobility received as a result of the intervention with accidental injury or exposure to infectious diseases, but rather with an increased sense of mental well-being as a result of their ability to socialise with family and friends despite their limiting ill health. Although some trial participants used their additional benefit income to afford a new car or taxi fares, trial participants felt that this increased, rather than limited, their levels of physical activity, as they were unable to leave the house without this transport available. No other potential unanticipated harms or risks were discussed throughout the qualitative study. There were, however, a number of unanticipated consequences concerning the intervention delivery identified by the WRAs delivering the intervention.

Impact of external factors

Throughout the period of the study, major changes to the UK welfare system were being implemented. Owing to the timing of the intervention delivery (June 2012 to August 2013), none of the changes [e.g. introduction of Universal Credit, Personal Independence Payments and the spare room subsidy (‘bedroom tax’)], affected our intervention trial participants. Overall, in comparison with the adult population below state pension age, those over the state pension age are less affected by the changes, in terms of the key benefits available to older people. However, the cuts in public services disproportionately affected the poorest areas with the worst health outcomes. Welfare rights advice services came under increasing strain from a combination of funding cuts and increasing demands as a result of changes to welfare. 106,107 Thus, the service delivery model that was developed and piloted in 2001–5,11 and that we adopted for the Do-Well study, had to operate under highly constrained budgeting circumstances. We therefore took these external factors into account and examined the suitability of our intervention delivery model in the current economic climate.

Summary

The findings of this embedded qualitative study indicate that the research design, in terms of recruitment and randomisation, was acceptable to those interviewed, although there was some concern expressed, primarily by professional informants, about the 24-month wait for the control group to receive the intervention. Without exception among trial participants the intervention was deemed acceptable. The professional informants supported the need for welfare rights advice targeted at older people, but there was some disagreement about the optimal means of service delivery, particularly in the light of recent and continuing cuts to public and voluntary sector services. Trial participants viewed the impact of the intervention as highly positive, in terms of financial, social, health and well-being factors, irrespective of the amount of additional benefit received; professional participants were fully aware of the wide-ranging impact that additional resources could have for older people in need, and reiterated the preventative potential of ‘low-level’ interventions such as welfare rights advice. The mechanisms of intervention delivery – introduced via trusted GPs and domiciliary visits – successfully overcame the well-known barriers to claiming benefit entitlements among older people. However, immediately before and during the execution of the trial the most significant government-led changes to the welfare system since its inception began to be implemented, coupled with austerity-driven public sector and voluntary sector service cutbacks. These external factors were perceived to have considerable implications for the design, commissioning and delivery of welfare rights advice services in the future.

Sample characteristics

Table 23 shows the responses to questionnaire data on individual health at baseline and 24-month follow-up for both trial arms. The majority of participants in both trial arms reported having a long-term illness, health problem or disability. At both baseline and 24-month follow-up, and for both trial arms, the largest proportion in each arm described their health status over the previous 6 months as good. The proportion in each arm reporting a long-term illness, health problem or disability, and a health problem limiting their daily activities, decreased over the 24 months of the trial. However, comparing the average baseline EQ-5D-3L score for those participants with missing EQ-5D-3L at 24-month follow-up with the average score for the complete study population showed that those with missing follow-up data had reported a substantially lower EQ-5D-3L at baseline [intervention group 0.589 (complete study population) vs. 0.529 (participants with missing 24-month follow-up EQ-5D-3L score); control group 0.583 vs. 0.457].

Cost–consequences analysis

Cost–utility analysis

On average, the (adjusted) intervention was found to be more costly and more effective than usual care (Table 34).

However, the differences in QALYs gained were not significant (p = 0.966). The point estimate of incremental cost per QALY gained was £1914. Nevertheless, there is considerable statistical imprecision surrounding these data, and bootstrapping was used to estimate the precision surrounding estimates of cost, QALYs and incremental cost per QALY. The incremental cost-effectiveness plane (Figure 6) visually plots the differences in mean costs and effects from each of the 1000 bootstrap iterations and indicates the level of uncertainty around cost and QALY point estimates (as previously reported by the 95% bootstrapped CIs in Table 34). Every point above the x-axis indicates that the intervention is more costly than usual care. Every point left of the y-axis indicates that the intervention is less effective than usual care, and right of the y-axis is more effective.

FIGURE 6.

Cost-effectiveness plane.

The statistical imprecision surrounding estimates of cost-effectiveness are presented in terms of a CEAC (Figure 7). A CEAC shows the one-sided probability that the intervention is cost-effective at any given value for society’s WTP for a QALY gained. This is analogous to the upper interval in a CI; the lower interval is irrelevant if we believe that the intervention is cost-effective at the upper interval because it must therefore be cost-effective at the lower interval.

FIGURE 7.

Cost-effectiveness acceptability curve.

In the CEAC we calculate the number of bootstrap iterations where the intervention arm is likely to be considered cost-effective compared with control over a range of values for society’s WTP for a QALY gain. As we have 1000 bootstrap iterations, we can estimate the probability that the intervention is cost-effective over the range of values. Furthermore, if the intervention is not cost-effective compared with the control then the control is cost-effective.

The probability that the intervention would be cost-effective, should society be willing to pay £20,000 per QALY gained, was around 63%. This suggests, given current evidence, that in economic terms and taking a NHS and local authority perspective we are almost indifferent to whether or not the intervention is implemented.

From an individual perspective, however, the value of the benefits can be considered a gain, albeit one that has not clearly translated into improved health over the 2-year time horizon of the study.

These results were robust to changes in the discount rate and higher costs associated with the delivery of the intervention.

The base-case analysis was based on complete cases. When missing EQ-5D-3L data were imputed using multiple imputation, the QALYs gained in the control group were, on average, 0.019 higher (95% CI –0.068 to 0.029). Therefore, the intervention was, on average, more costly and less effective than the control, and hence the intervention was dominated by usual care (Table 35).

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.

Contributions of authors

Catherine Haighton (Lecturer, Public Health) contributed to the study design and the development of methods, managed the project overall, helped with the data analysis and interpretation, and drafted text in the report.

Suzanne Moffatt (Senior Lecturer, Sociology of Health and Illness) conceived the idea for the study, contributed to the study design and the development of methods, led the embedded qualitative study, helped with the data analysis and interpretation, and drafted text.

Denise Howel (Senior Lecturer, Statistics) conceived the idea for the study, contributed to the study design and the development of methods, led the statistical analysis for the main trial, contributed to the data analysis and interpretation, and drafted text.

Mel Steer (Research Associate) conducted qualitative interviews, contributed to the data analysis and interpretation, and drafted text.

Frauke Becker (Research Associate, Health Economics) contributed to the methods development, collected economic data, conducted the economic analysis, contributed to the data interpretation and drafted text.

Andrew Bryant (Research Associate, Statistics) conducted the statistical analysis for the main trial and contributed to the data interpretation.

Sarah Lawson (Research Associate, Qualitative Research) conducted qualitative interviews, contributed to the data analysis and interpretation, and drafted text.

Elaine McColl (Professor, Health Services Research) contributed to the study design and methods development, oversaw research governance and contributed to the data interpretation.

Luke Vale (Health Foundation Chair, Health Economics) contributed to the methods development, led the economic evaluation, contributed to the data analysis and interpretation, and drafted text.

Eugene Milne (Director, Public Health) contributed to the study design, provided liaison with public health stakeholders and contributed to the data interpretation.

Terry Aspray (Consultant, Geriatric Medicine) contributed to the study design and data interpretation.

Martin White (Professor, Public Health) was chief investigator with overall responsibility for the study, conceived the idea for the study, contributed to the study design and methods development, oversaw the fieldwork, contributed to the data interpretation and drafted text.

All authors commented on drafts of the report and approved the final version.

Emma Noble (deceased) (Research Associate, Public Health) contributed to the development of methods and carried out fieldwork at baseline and at 12-month follow-up.

Publications

Data-sharing statement

All data requested shoud be submitted to the corresponding author for consideration. Access to available anomymised data may be granted following review.

Disclaimers

This report presents independent research funded by the National Institute for Health Research (NIHR). The views and opinions expressed by authors in this publication are those of the authors and do not necessarily reflect those of the NHS, the NIHR, NETSCC, the PHR programme or the Department of Health and Social Care. If there are verbatim quotations included in this publication the views and opinions expressed by the interviewees are those of the interviewees and do not necessarily reflect those of the authors, those of the NHS, the NIHR, NETSCC, the PHR programme or the Department of Health and Social Care.