Abdominal massage plus advice, compared with advice only, for neurogenic bowel dysfunction in MS: a RCT

Article history

The research reported in this issue of the journal was funded by the HTA programme as project number 12/127/12. The contractual start date was in July 2014. The draft report began editorial review in July 2017 and was accepted for publication in March 2018. The authors have been wholly responsible for all data collection, analysis and interpretation, and for writing up their work. The HTA editors and publisher have tried to ensure the accuracy of the authors’ report and would like to thank the reviewers for their constructive comments on the draft document. However, they do not accept liability for damages or losses arising from material published in this report.

Declared competing interests of authors

Maureen Coggrave reports personal fees from Hollister Incorporated (Libertyville, IL, USA) and Wellspect HealthCare (Weybridge, UK), both outside this study. John Norrie was a member of the National Institute for Health Research (NIHR) Commissioning Board from 2010 to 2016, is currently an editor on the NIHR Journals Editorial Board and is Deputy Chairperson of the NIHR Health Technology Assessment General Board. Peter Donnan reports grants from Shire plc (Dublin, Ireland), Novo Nordisk A/S (Bagsværd, Denmark), GlaxoSmithKline plc (London, UK), AstraZeneca plc (Cambridge, UK) and Gilead Sciences Inc. (Foster City, CA, USA), outside this study. He is also a member of the New Drugs Committee of the Scottish Medicines Consortium.

Copyright statement

© Queen’s Printer and Controller of HMSO 2018. This work was produced by McClurg et al. under the terms of a commissioning contract issued by the Secretary of State for Health and Social Care. 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.

2018 Queen’s Printer and Controller of HMSO

Scientific background

The prevalence of multiple sclerosis (MS) is increasing in the UK, and MS is the most common neurological condition in young adults (the average age at onset is 34 years), affecting > 100,000 people at present. 1 It is estimated that 60% of people with multiple sclerosis (PwMS) have problematic neurogenic bowel dysfunction (NBD);2 increased life-expectancy rates, as a result of advances in health care, present additional challenges of the ageing bowel. 3 NBD is rated as one of the most distressing scenarios affecting these patients and includes the symptoms of constipation and faecal incontinence (FI). 4 Constipation can lead to the individual becoming housebound, spending hours trying to empty their bowels and limiting their ability to work; whereas FI is often described as the most devastating event imaginable, leading to social and emotional issues. 5 A MS Trust report6 published in April 2017 revealed that emergency admissions (many of which are thought to be preventable) to hospital for PwMS have increased by 12.7% over the 2 years 2015/16, with overall admissions for bladder- and bowel-related issues, for example impaction, costing £10.4M in 2015/16.

Aetiology of neurogenic bowel dysfunction

Aetiology of NBD in PwMS is multifactorial; reduced mobility and polypharmacy may have a contributory causative role. Coincidental pelvic nerve lesion, occurring during childbirth, could also contribute to FI in women with MS. 7 Spinal cord lesions appear to be most important in the pathogenesis of NBD symptoms in MS. 8 The pathways of neural control of defecation are not fully defined; however, cortical and pontine centres may play a pivotal role in the regulation of sacral segments. 8,9

Conduction times of central motor pathways to sphincteric sacral neurons and pelvic floor striated muscle have been shown to be prolonged in MS. 10 Impaired anorectal sensation may also contribute to the symptoms; somatosensory-evoked potentials were delayed in PwMS compared with controls in one study. 11 Loss of central modulation on spinal cord segments may lead to sympathovagal imbalance, which, in turn, can lead to constipation, characterised by lengthened colon transit time. 12 Constipation has thus been attributed to rectal outlet obstruction, absent or incomplete puborectalis, anal canal and sphincter musculature relaxation, and prolonged colonic transit time. 10,13 Regarding FI, studies have described reduced sensation of rectal filling, reduced rectal compliance, low anal sphincter pressures and hyper-reactivity of the rectal wall. The coexistence of FI and constipation can be explained by inco-ordinated action of the external/internal anal sphincter during expulsion; poor pelvic musculature relaxation may cause incomplete emptying of the rectum, which precipitates FI when anal sphincter weakness and anorectal hyposensitivity are present. 14,15

Current treatment/management options

Management of NBD in PwMS has been little explored and lacks supporting evidence. 16 It is costly both in terms of patient time and to the NHS (e.g. PwMS have two to three times more admissions to hospital for bowel complications than non-MS patients). 17 It also has an impact on the families and carers of PwMS. 18 PwMS use laxatives, suppositories, prolonged digital rectal stimulation and/or rectal irrigation, but often these interventions have inconsistent results. For example, one patient in our previous study would take laxatives two evenings per week, but then could not leave the house the next day as he had no control over when he would pass stool. 5

Evidence for the clinical effectiveness of abdominal massage for constipation

A Cochrane systematic review19 has been undertaken to determine the effects of abdominal massage for the relief of symptoms of chronic constipation in comparison with no treatment or other treatment options. Nine randomised controlled trials (RCTs) (12 randomised comparisons) involving 427 participants were included in the review. 19 The study populations were small (with a maximum of 32 participants per group), heterogeneous and all were rated as having a moderate or high risk of bias. Findings from two trials suggested that abdominal massage compared with advice from a physician provided significant additional relief of symptoms from constipation in the short term. Two trials found no significant differences between groups. One trial, which had the three groups (aroma massage, plain massage and control), reported that both the aroma massage group and the plain massage group had an improved quality of life. The review concluded that there were insufficient data to allow reliable conclusions to be drawn on the effects of abdominal massage in the management of constipation. There was some evidence to suggest that there might be a therapeutic effect; however, larger, more rigorous trials are required to provide evidence of both the clinical effectiveness and the cost-effectiveness of abdominal massage.

How the intervention might work

There is some evidence to suggest that abdominal massage will reduce colonic transit time and enable predictable complete evacuation; however, the possible mechanism of action is not yet fully understood. 20,21 The function of the gastrointestinal tract is influenced by, among other things, activity in the parasympathetic division in the autonomic nervous system. Stimulation of the parasympathetic division increases the motility of the muscles, increases the digestive secretions and relaxes sphincters in the gastrointestinal canal. 22–24 Massage is thought to stimulate peristalsis in the gut by producing rectal muscular waves that stimulate the somatoautomatic reflex and initiate bowel sensation, thereby reducing colonic transit time. 25 Furthermore, the active massaging action may result in a softening of stool consistency, allowing the stool to be passed more easily. 26

Development of the intervention

The abdominal massage intervention used within this trial was based on massage as formally taught in physiotherapy training within the UK and used by an expert in the area in earlier studies. 27–29 This expert was involved in the development of the training materials and in the training of the clinicians undertaking the massage. All clinicians involved with teaching the massage to participants underwent 1 half day of training in the massage technique, as well as presentations on NBD and good bowel care. Information provided to participants on bowel care was based on the MS Society’s handbook on bowel management. A description of the intervention has previously been published. 30 A copy of the training materials is available in Appendix 1.

Who delivers the intervention

In previous studies, the massage was delivered by a health-care professional (HCP) with experience in massage, a family carer or by the patient themselves. It was discovered, however, that the amount of training and support received by participants is poorly described. In this trial, the massage was designed and taught to be either self-massage or undertaken by a ‘carer’. Likewise, the training of the ‘trainers’ (HCPs involved in seeing the patient and teaching the massage) was such that it was delivered in one half-day session, but also required individuals to undertake further practice, to consolidate their training. If this limited training plus support materials for HCPs and patients were to prove effective, then the abdominal massage could potentially be implemented in many settings to patient populations who experience constipation.

Hypothesis

A 6-week intervention of abdominal massage and bowel management advice (intervention group) will improve symptoms and quality of life in PwMS who have NBD compared with advice alone (control group).

Ethics approval and research governance

Ethics approval for the trial was granted by the West of Scotland Research Ethics Committee (REC) 4 on 11 June 2014 (reference number 14/WS/0111). NHS approval was granted for 10 different trusts/foundation trusts in England, and two local health boards granted approval for the two sites in Scotland. The trial sponsor was Glasgow Caledonian University (GCU) and the AMBER trial office was based in the Nursing, Midwifery and Allied Health Professions Research Unit (NMAHP RU) at GCU. The AMBER trial was registered with the International Standard Randomised Controlled Trial Number (ISRCTN) registry (ISRCTN85007023) and on ClinicalTrials.gov (NCT03166007).

Participants

The trial recruited PwMS who reported that they were ‘bothered’ (in their own judgement) by their NBD symptoms at 12 sites across UK (n = 2 in Scotland and n = 10 in England).

Recruitment procedure

The research team at each trial site were responsible for identifying potential participants. Following identification of potentially eligible individuals, a letter of introduction and an ‘expression of interest’ form was either posted or given to patients at their routine clinic appointment. Each patient approached about the trial was allocated a unique participant identifier number. This consisted of six characters: three letters that were an abbreviation of the site name followed by three numbers that were allocated on a consecutive basis (e.g. 001 for first participant). This unique identifier was used throughout the trial and was added to all participant paperwork. Once a completed ‘expression of interest’ form was returned, a member of the research team telephoned the individual to provide further information and assess eligibility. If eligible and willing to take part, the individual was sent a baseline appointment letter along with a 7-day bowel diary for completion. The participant completed the bowel diary the week before the baseline appointment. Participants were also asked to bring someone who was willing to do the massage to this appointment, if required.

Informed consent

Informed, written consent was obtained for all participants at the baseline appointment and included consent to any site-specific tests. The REC agreed to the completion of bowel diaries before the baseline appointment, as the participants’ consent was implied by them willingly completing the diary. There was no use of these data until participants had provided written informed consent; this method aided recruitment to the trial because it meant that there was only one clinic visit required. Participants were made aware that the treatment was allocated at random, regardless of any personal preference they had. They had the right to withdraw from the trial at any time and for any reason; all participants were also made aware that withdrawal would not affect their routine care.

The consent form also had the option for the participant to be contacted if they were interested in taking part in the process evaluation interviews. Chapter 5 explains the consent method followed for this part of the study. The general practitioners (GPs) of all those who took part in the trial were informed of their involvement.

Randomisation, concealment and blinding

Participants who provided written informed consent were randomly allocated to one of two treatment groups during their baseline appointment: (1) advice to optimise bowel care (control group) or (2) advice to optimise bowel care and abdominal massage (intervention group). The web-based randomisation service was provided by the Tayside Clinical Trials Unit (CTU), a UK Clinical Research Collaboration (UKCRC)-registered trials unit, and research staff at sites carried out the randomisation. In a few instances, the AMBER trial central office would assist with the randomisation remotely. This took place when there may have been issues for the staff when connecting to the web-based randomisation system (room allocation with no computer or web connectivity issues). Group allocation was relayed by telephone to the site and copies of the relevant randomisation paperwork were sent to all of those involved. Owing to the nature of the intervention, it was not possible to blind the participants or site staff to the allocation. Participant group allocation was unknown to the data analysis team. Randomisation was stratified by site and minimised on level of disability (walking unaided, aided or wheelchair bound).

Treatment group allocation

Intervention group (abdominal massage and advice to optimise bowel care)

In addition to optimised bowel care as described for the control group, staff delivering the intervention (local HCPs all fully trained in the massage technique) taught the participant and/or his or her carer how to deliver the abdominal massage. This teaching included the following:

• Viewing a short trial-specific digital versatile disc (DVD) that demonstrated the massage techniques for carer and self-massage (Figure 1 shows a picture captured from the training DVD).

• Provision of a study-specific abdominal massage training booklet.

• A demonstration of the massage technique on the participant.

• Practice of the various strokes by the carer or participant.

• An opportunity for the participant and carer to ask questions. Possible adaptations to accommodate a participant’s disability were also discussed. A daily massage of 10 minutes duration was recommended.

FIGURE 1.

A picture from the AMBER trial training DVD, which demonstrates the massage strokes to be used.

Participants in this group were given an information pack that consisted of the following:

• the MS Society’s bowel care advice booklet

• the massage DVD

• patient abdominal massage training information leaflets.

In order to standardise the intervention delivery across all sites, training for all site staff delivering the intervention was provided by one individual with clinical expertise in the area. Staff attended a trial training day and/or they were trained during the site initiation visits. Each staff member had to perform practical demonstrations and be deemed proficient in the technique before being signed off as fully competent. Sites were contacted after the baseline appointment of their first participant from the intervention group to discuss how staff found delivering the massage and to answer any questions. Further training was available at this point, but all sites felt confident in the delivery of the intervention. Any questions/feedback from the individual sites were shared with all research site staff via monthly update teleconferences. The weekly telephone calls to participants were done either by the staff member who delivered the massage training, or by another member of staff on the delegation log.

Participants randomised to the control group were informed that they would be given access to the massage training materials at the end of their follow-up (week 24). In addition, some of the sites offered to hold training sessions with the control group participants after they had completed the study.

A description of how to perform the massage technique can be found in Appendix 1, along with the training material given to participants as an aide memoire.

Mechanistic evaluation

One of the sites in the AMBER trial [University College Hospital (UCH), London] is a regional NBD centre where standard anorectal physiology and colonic transit tests are routinely undertaken. AMBER trial participants recruited at this site underwent the following tests before the intervention, and then again at 24 weeks:

• Anorectal pressure test – this test involves the insertion of a small probe into the rectum to measure the strength of the anal muscles.

• Anal and rectal sensation and capacity was measured by using a tiny amount of current and inflating a small balloon within the rectum (a balloon was inserted via a tube, and sensory thresholds to progressive distension were established. The initial tube was then removed and a different catheter with a bipolar electrode inserted; the sensory threshold to 1 mA of current was then determined).

• Transit tests – three sets of radiopaque capsules were posted to the participant, who ingested them in the order specified in the instructions on 3 consecutive days. Participants then attended for an abdominal radiography 2 days after the last capsule to determine total colonic transit time (not segmental transit).

This was a small substudy in the AMBER trial to look at possible mechanisms involved in NBD in PwMS and to look at the feasibility of undertaking such tests within this population and their compliance with attending the repeat tests.

Data collection and management

Data were collected and recorded on study-specific paper-based case report forms (CRFs) by either site staff or the participants (bowel diaries and patient-reported outcomes during weeks 1–6 and week 24). Sites were trained on completion of all the paperwork before recruitment commenced and a monthly teleconference, with all sites jointly, allowed any data issues/inconsistencies to be discussed and resolved. The AMBER trial central office entered all data into the OpenClinica database (OpenClinica, LLC, Waltham, MA, USA). This was set up and managed by Tayside CTU. A range of data validation checks was used to minimise erroneous and missing data.

Baseline assessment

Demographic data and information on participants’ MS, medical history and bowel symptoms were collected at the baseline assessment. Participants also completed a questionnaire booklet which contained five different questionnaires (including the primary and secondary outcome measures – see Outcome measures and Appendices 2 and 3). Information on current medication was recorded, including any laxative use. Participants were given the bowel diaries and questionnaires, which were to be completed during the 6-week intervention phase, at the baseline assessment, with an instruction sheet detailing how they should be completed. Baseline anorectal physiology and colonic transit time data were collected from the London participants using an anorectal physiology CRF.

Baseline assessments were conducted between 22 January 2015 and 19 July 2016.

Participant follow-up

The duration of follow-up was 24 weeks from the date of randomisation.

Outcomes were collected through the following documents, which were completed by participants:

• a questionnaire booklet at weeks 6 and 24 (the same as the baseline questionnaire)

• a 7-day bowel diary (control group) or bowel and massage diary (intervention group) at weeks 1 to 6 and during week 23

• patient resource-use questionnaires at weeks 1–6, and weeks 12, 18 and 24.

All information completed by the participants was returned to the AMBER trial central office by reply-paid envelopes that were provided.

Anorectal physiology and colonic transit time data were collected at week 24 in UCH participants only.

Site research staff telephoned all participants weekly during weeks 1 to 6 and again at week 24 to collect additional information on any potential issues, changes in diet/exercise/fluid, adverse events (AEs) and any changes in medication. Any potential issues with bowel management or the massage were discussed and fed back to the AMBER trial central office if deemed necessary.

All AMBER trial follow-ups were completed by 19 January 2017.

Table 1 shows the AMBER trial matrix and data collected at each time point.

Outcome measures

Change of medication

Changes of medication were recorded using a current medication form. Any changes to a participant’s medications during their involvement in the trial were recorded. Also recorded were any reductions or stoppage of laxatives between baseline and week 24.

Radiopaque marker transit tests

Different parameters were collected on an anorectal CRF (see Report Supplementary Material 1) for the physiology and transit tests. The total number of markers remaining in the gut at abdominal radiography was analysed to determine any differences between baseline and week 24, and all other data were summarised.

Adverse events

Expected AEs arising from the treatments in the AMBER trial are noted below. These are common in individuals with constipation and thus were not collected as AEs but noted in the weekly follow-up data collection:

• increased flatulence

• abdominal cramps

• stomach rumblings/noises

• loose stool, which in some instances may lead to faecal incontinence.

All AEs (for which a participant sought intervention from a HCP) and SAEs (including death, life-threatening conditions, inpatient hospitalisation or prolongation of existing hospitalisation and persistent or significant disability or incapacity) were assessed for causality, severity and expectedness, and were reported to the relevant regulatory bodies. If a site was in doubt about whether or not an event was an AE, this was reported and discussed before data lock. Any AE that was deemed as ongoing at the end of the trial was reviewed and further clarification from the site was sought. If the AE was still ongoing after this (owing to the nature of the event, but not related to the intervention), this was when the follow-up ended.

Adverse events (including SAEs) were coded with the Medical Dictionary for Regulatory Activities (MedDRA)36 16.1 and reported by primary System Organ Class (SOC) and preferred term (PT). Participants were counted only once when calculating the incidence of AEs. An overview table was created counting the number of AEs by SOC and PT.

Sample size

The sample size for the RCT was based on the NBDS, using data from a pilot study37 that provided the only published data available on abdominal massage in this group of patients. That study37 found a difference of 4.21 points in the NBDS between those receiving the intervention {mean score of 6.86 points [standard deviation (SD) 3.8 points] at 8 weeks} and the comparison group [mean score of 11.07 points (SD 7.02 points) at 8 weeks]. Other outcomes in that study changed in favour of the intervention and participants anecdotally reported that the massage was relaxing and that they were keen to do it themselves. Using these data, we selected a minimum clinically important difference (MCID) of 4.21 points and selected the higher SD of 7.02 points, found in the comparison group, as the basis for our sample size calculation.

Using these data, 60 participants per group was calculated as the necessary number of participants to detect a difference between groups of 4.21 points (SD 7.02 points) at a 5% level of significance with 90% power. Thus, for a fully powered study, the total sample size, allowing for a 20% dropout rate, was 150. However, in response to suggestions from the funding body, the sample size was increased to 200 participants (100 per group), which allowed for greater attrition.

Statistical analyses

Statistical methods for analysis of the main primary and secondary outcomes are detailed in the following sections. This document was drawn up by the trial statisticians, reviewed by the Project Management Group and formally signed off by the chief investigator and trial statistician before analysis commenced.

Analysis populations

Analysis was performed for the intention-to-treat population and is reported in accordance with Consolidated Standards of Reporting Trials (CONSORT). 38

Subgroups

Subgroup analyses were carried out by first testing for a subgroup factor by intervention interaction. If this was significant at the 5% level, results were estimated separately by the different subgroups. This included a secondary analysis comparing those who undertook the massage themselves with those who had a carer massage them.

Missing data

The extent of missing data was explored in the outcomes, especially the primary outcome. Patterns of missing data were explored and predictors of missingness examined, especially if these varied by intervention. A table was constructed to assess differences in characteristics of those with complete data and those with missing data for the primary analysis. Multiple imputation (MI) was implemented for the primary outcome, assuming data were missing at random.

Summary of trial data

All continuous variables were summarised using the following descriptive statistics: non-missing sample size, number of missing records, mean, SD, median, maximum and minimum. The frequency and percentages (based on the non-missing sample size) of observed levels were reported for all categorical measures. In general, all data were listed, sorted by subject and treatment and, when appropriate, by visit number within subject.

All summary tables were structured with a column for each treatment group and an additional column for the total population relevant to that table/treatment, including any missing observations.

Demographic and baseline variables

The baseline characteristics of participants that were recorded comprised age, sex, body mass index (BMI), type of MS, site, number of years since diagnosis, cognitive symptoms of MS and level of mobility (walking unaided, aided or wheelchair bound).

Prior and current medications

Prior medications were all medications that were being taken by a participant before the trial started. Concomitant medications were all medications commenced during the trial and all changes to the dosing of prior medications. Prior medications were listed but not analysed. Concomitant medications were analysed by number of medications taken.

Treatment adherence

Treatment adherence was calculated from the weekly bowel diaries. The number of times the bowel massage was done per week was used in the main analysis. For the control group, this number was set to 0.

Efficacy analyses

Data for continuous outcome measures (both primary and secondary) were assessed for normality before analysis. Transformations of the outcome variables were used when necessary, if these were not normally distributed.

If data were normally distributed, outcome measures were assessed by multiple linear mixed-model regression. The primary analysis consisted of comparisons between treatment groups (bowel massage vs. no massage) at the final visit (week 24), adjusted for site, minimisation variable level of mobility (walking unaided, aided or wheelchair bound), as well as baseline measure of the outcome and sex.

In a secondary analysis of the primary outcome, additional baseline variables (age, sex, BMI, type of MS, number of years since diagnosis and cognitive symptoms of MS) were included in the model.

When data were not normally distributed and could not be transformed into a normal distribution, they were analysed using non-parametric methods in addition to multiple linear regression.

In addition to the comparison of baseline with week 24, a repeated measures mixed-model analysis was performed on the outcomes using all available visits.

Data for categorical outcome measures were assessed by logistic regression in the same way as described for continuous outcome measures.

Reporting conventions

Values of ≥ 0.001 are reported to three decimal places; p-values of < 0.001 are reported as < 0.001. The mean, SD and any other statistics, other than quantiles, are reported to one decimal place greater than the original data. Quantiles, such as median or minimum and maximum, use the same number of decimal places as the original data. Estimated parameters not on the same scale as raw observations (e.g. regression coefficients) are reported to three significant figures.

All analyses were performed using SAS^® 9.3 (SAS Institute Inc., Cary, NC, USA. SAS and all other SAS Institute Inc. product or service names are registered trademarks or trademarks of SAS Institute Inc. in the USA and other countries. ^® indicates USA registration.) All data, analysis programs and output were kept on the Mackenzie Server and backed up according to the internal Tayside Clinical Trials Unit (TCTU) information technology standard operating procedures.

Analysis programs were required to run without errors or warnings. The analysis programs for outcomes were reviewed by a second statistician and any irregularities in the programs were investigated and fixed, and the date of finalised analysis programs was signed and recorded.

Economic analysis

The cost of abdominal massage and optimised bowel care relative to optimised bowel care alone in PwMS who have NBD was considered from NHS and patient perspectives. Health-care resource use by patients in both trial groups was collected at each of the follow-up time periods (weeks 1–6, 12, 18 and 24). This included contact with health professionals and medications prescribed. These were costed using NHS pay and prices or, when appropriate, other (e.g. market-based) sources. The economic analysis (including the methods used) is detailed in Chapter 4.

Important changes to protocol after trial commencement

All sites used protocol version 2, dated 18 November 2014, throughout the trial duration. The London site used an additional patient information leaflet (PIL) to describe the additional tests carried out at this site. After original approval of the PIL, one of the tests was no longer completed routinely at the London site, so this information was removed and the amended PIL was approved by all relevant regulatory bodies. This change was carried out before any patients were recruited at the site.

Another substantial amendment was to incorporate a substudy, entitled SWAT (study within a trial) 24, in the AMBER trial. Participants were randomised to receive either the original cover letter or an enhanced cover letter (sent with the questionnaire at week 24) to evaluate whether or not the wording used would increase return rates of the questionnaires.

Data from the substudy will contribute to the Trial Forge39 initiative to improve trial efficiency and to the Cochrane review of strategies to improve trial retention. 40

The results of the Trial Forge39 project will help to increase the evidence base on the retention of participants to trials. The only change to the AMBER trial was the way that the cover letter sent with questionnaires was written (no protocol change).

Other non-substantial changes included the:

• addition of new sites as the trial progressed (original target was 10 sites but final total was 12 sites)

• set-up of two patient-identifying centres to assist two sites with recruitment

• sites collecting the NBDS during the telephone call with participants at week 24 to maximise the primary outcome data in the study.

Trial oversight

The trial was led by the chief investigator who, along with the trial management team members (consisting of a trial manager, a data co-ordinator and a process evaluation researcher), were employed by NMAHP RU.

The trial was overseen by a Project Management Group (PMG), a Trial Steering Committee (TSC) and a Data Monitoring and Ethics Committee (DMEC).

The PMG had a teleconference approximately every 4–6 weeks during the recruitment period and then bimonthly after this. The group’s role was to support any decision-making that the trial management team needed further advice on.

The TSC had both an independent chairperson and members but also consisted of the trial collaborators. The TSC had four meetings over the course of the trial, with additional updates on recruitment when requested. The TSC commended the team on recruiting to target and on time.

An independent DMEC, chaired by a statistician, had three meetings over the course of the study, and additional updates were provided when requested. All statistical reports to the DMEC were prepared by a statistician from the TCTU. The DMEC had no issues with the trial continuing at any time point and commended the team on the recruitment and management of the study. The DMEC charter can be reviewed in Appendix 2.

Patient and public involvement

The AMBER trial has had active participation with a group of PwMS (hereafter referred to as the MS focus group). Some of the MS focus group were involved with the development of the grant application, providing feedback on the lay summary, trial design and appropriate outcome measures and questionnaires. Several additional PwMS became involved during the very early stages of the trial and throughout implementation and dissemination of results. The MS focus group included males and females, with various levels of disability and of various ages, some with and some without NBD. Approximately 10 members of the MS focus group attended each of the meetings. Material to review was sent electronically before the meetings and was available in hard copy at the meetings; very helpful feedback and discussions took place. One of the members of the MS focus group has also attended each TSC meeting as a lay representative and has actively engaged in the conversations and discussions at each meeting. Before recruiting any participants to the trial, the MS focus group reviewed the massage training DVD and the massage training material that would be given to the participant to take home with them, and their input to this was extremely influential. The group’s opinion of the initial version of the training DVD was that the visual was excellent but the language used was ‘too clinical’. This was overcome by the chief investigator of the trial doing a voice-over on the DVD; the group reviewed this again and it was deemed much more acceptable and user friendly. Many of the trial participants subsequently commented that they thought the video was extremely useful and easy to follow.

We initially had two different training documents and we asked the group which would be better used as an aide memoire. The MS focus group had very mixed opinions on their preferences, and discussed the style, language and diagrams used. It was therefore concluded that both of these additional training materials would be provided to all participants in the intervention arm and they could decide which material they felt was better for them. However, there is the possibility of combining the information into one single training document if the intervention is rolled out to clinical care.

Participants in the AMBER trial were given quite a lot of information to take away with them at the baseline appointment, in the form of a ‘follow-up pack’. This pack included all the questionnaires and bowel diaries and study instructions on what they had to complete over the 6-week intervention period, and also the massage training DVD and reading materials (only if the participant was in the intervention group). The MS focus group reviewed this pack and thought that it was logical and clear and some further feedback from site staff implied that the participants ‘liked’ having this pack to take away with them.

We kept in touch with the MS focus group throughout the study, giving updates on recruitment, and there were discussions on dissemination plans. A dissemination day was held on 23 January 2018 in Glasgow Caledonian University, to which all the research staff involved in the study, and local participants, were invited. Representatives of the MS focus group also attended.

Throughout the active recruitment of the study, local and national MS charities were aware of our research and promoted the study where regulations allowed.

Trial recruitment

Recruitment overall was considered very successful; Figure 2 shows how well the actual recruitment met the expected monthly targets over the 18 months of active recruitment. The trial oversight committees agreed to stop recruitment on time at 191 participants after reviewing attrition information. Twelve sites recruited participants from 22 January 2015 to 19 July 2016 and each site recruited between 9 and 26 participants (see Appendix 3).

FIGURE 2.

Predicted recruitment vs. actual recruitment.

The CONSORT flow diagram (Figure 3) shows the movement of participants through the AMBER trial. There were 237 PwMS and possible bowel problems screened (≈61% of the 389 PwMS approached by the research staff) and 191 PwMS (81% of those screened; 49% of those approached) were randomised. The near 50% uptake on those approached versus those randomised was in accordance with the estimate of uptake stated in the protocol.

FIGURE 3.

The CONSORT flow diagram. Qu, questionnaire. a, In the enrolment and screening information, all percentages are calculated from the number of people approached about the study (n = 389); b, reasons for those who were eligible but did not take part vary from a patient’s personal circumstances changing to baseline appointments being made for a patient but he/she not attending; c, in each group, one participant was randomised and subsequently deemed ineligible for the trial when eligibility was reassessed. No data were collected for these two participants; and d, these sections show the breakdown for the primary outcome measure (NBDS) at each stage of data collection: baseline, week 6 and week 24. All percentages calculated are from n = 90 (intervention group) and n = 99 (control group).

Of the randomised participants, 22 did not complete the study. Two of these were post-randomisation exclusions (essentially randomised in error) and data were not collected from these two participants. Thus, the analysis was based on 189 participants: 90 in the intervention group (abdominal massage plus advice on optimised bowel care) and 99 in the control group (only advice on optimised bowel care). The inequality in the number of participants per group was attributable to minimisation at site level.

For the 20 correctly randomised participants (intervention group, n = 15; control group, n = 5) who did not complete the study, baseline data were successfully collected and all participants agreed that their existing data could be used. Participants either withdrew (intervention group, n = 11; control group, n = 3) or were lost to follow-up (intervention group, n = 4; control group, n = 2). In some instances, if the data were not returned, then the week-6 and week-24 follow-up data collection was completed by the researcher during a telephone call. This explains the differing numbers for the NBDS in the CONSORT flow diagram at weeks 6 and 24 in relation to reported withdrawals or loss to follow-up.

Quality of participant-completed outcome data

Participant-completed outcomes were returned by post at weeks 6 and 24. Questionnaire and bowel diary data were checked for completeness and every effort was made to collect any missing information when acceptable to do so.

The CONSORT flow diagram (see Figure 3) shows the numbers available for the primary outcome analysis at baseline and weeks 6 and 24 (NBDS). During monitoring of the study attrition rates and primary and secondary outcome data received, it was evident that some participants were stating that they had returned their outcome measures by post but these were not received in the AMBER trial office. Thus, in order to maximise our available primary outcome data for analysis, from 22 March 2016 onwards, the research staff at each site completed the NBDS (10 questions) during the telephone call at week 24. This increased our available data for primary outcome analyses at 24 weeks, compared with 6 weeks, in both study groups (intervention group, 76.7%; control group, 84.8%).

There was a greater number of withdrawals/losses to follow-up in the intervention group (15/90) than in the control group (5/99).

For all outcome data, the numbers available for analysis and any reasons for missing data will be reported when discussing each outcome below.

Reasons for withdrawal/losses to follow-up

There were two randomisation failures and 20 participants who withdrew and were lost to follow-up (n = 14 intervention group, n = 16 control group; none withdrew consent for use of existing data). We have undertaken an analysis of the missing data (see Appendix 4) and it would seem that they do not suggest any major biases in the primary analysis. The reasons for withdrawal in the intervention group were varied and included change in diagnosis of MS, family circumstances, worsening of condition and too much paperwork. There is also the possibility that those in the control group remained in the study so that they would receive the training in the abdominal massage and had not yet experienced the potential disappointment of the intervention not working for them, which might increase the likelihood of withdrawing from the study. Interestingly, of those who took part in the interview study, none withdrew or were lost to follow-up, which may indicate that this was a more motivated group or that taking part in the interviews facilitated retention.

Missing primary outcome data

The missingness of the primary outcome data appeared to be relatively unrelated to baseline characteristics, apart from the following: trial group (more missing data in the intervention group), more missing data in those not wheelchair bound, slightly more missing data for women and for younger participants, and more missing data in some centres (see Appendix 4 and Chapter 6 for possible reasons for all of the above). However, using the characteristics at baseline to impute missing data, MI was carried out for the primary outcome and the primary analysis was repeated as a sensitivity analysis. This approach assumes that data are missing at random; this is discussed further in Chapter 6.

Baseline data

The mean age of participants was 53 years (SD 10.4 years) and 81% (154/189) were female. Mean time since diagnosis of MS was 14.3 years (SD 9.1 years). Baseline demographics and clinical data are summarised in Table 2. Demographics and symptom characteristics of the two groups were comparable at baseline.

Bowel symptoms

To be eligible to participate in the trial, participants had to be ‘bothered’ by their constipation. Bowel symptoms had commenced > 10 years ago in 37% of participants and < 1 year ago in 4% of participants. The main bowel symptoms reported by participants at baseline were a feeling of incomplete emptying, straining to pass stool and bloating (Table 3).

Primary analyses

The primary analysis is the comparison between treatment groups (bowel massage vs. no massage) at the final visit (24 weeks), adjusted for site and minimisation variable level of mobility (walking unaided, walking aided, or wheelchair bound), as well as baseline measure of the outcome and sex.

Primary outcome measure

Neurogenic Bowel Dysfunction Score

At baseline, the mean score for the intervention group was 7.6 points (SD 5.31 points) and the median was 6.0 points (range 0–21 points). For the control group at baseline, the mean NBDS was 8.6 points (SD 5.08 points) and the median was 9.0 points (range 0–22 points) (Table 4). These scores indicate that the NBD symptoms were having a minor impact on most participants. Scores of 7–11 points indicate minor impact and scores of ≥ 14 points indicate severe impact. The mean NBDS at week 24 was 7.4 points (SD 5.23 points) and the median was 7.0 points (range 0–24 points) for the intervention group; the mean NBDS was 8.7 points (SD 5.70 points) and the median was 7.5 points (range 0–24 points) for the control group at week 24. The mean adjusted difference in change between randomised groups from baseline to week 24 was not statistically significantly different [mean difference between groups (intervention – control): –1.6, 95% confidence interval (CI) –3.32 to 0.04; p = 0.0558; Table 5]. Figures 4 and 5 visually show the change over time within the two groups.

TABLE 4 - Summary of primary and secondary outcomes at baseline, week 6 and week 24

QoL, quality of life; VAS, visual analogue scale.

NBDS range: 0–47 points; a score of ≥ 14 points indicates severe NBD.

Constipation Scoring Symptom range: 0–30 points; a score of 30 points indicates severe constipation symptoms.

SF-Qualiveen total bladder score range: 0–4; a higher score indicates worse bladder dysfunction.

EQ-5D-5L VAS: maximum score of 100. A higher score indicates better QoL.

EQ-5D-5L health index: maximum score of 1, which indicates best health.

NBIS: higher scores for all subscales indicate greater improvement in NBD.

Score	Trial group
	Intervention (N = 90)				Control (N = 99)
	Mean (SD)		n	Median (range)	Mean (SD)		n		Median (range)
Primary outcome measure – symptom severity
NBD score (points)a
Baseline	7.6 (5.3)		86	6 (0–21)	8.6 (5.1)		94		9 (0–22)
Week 6	8.4 (6.2)		62	7 (0–25)	9.1 (5.7)		83		8 (0–34)
Week 24	7.4 (5.2)		69	7 (0–24)	8.7 (5.7)		84		7.5 (0–24)
Secondary outcome measure – symptom severity
Constipation score (points)b
Baseline	11.7 (4.1)		88	12 (1–25)	11.5 (3.8)		97		11 (3–21)
Week 6	10.6 (4.3)		58	11 (1–22)	10.8 (4.0)		83		11 (1–22)
Week 24	10.1 (4.1)		57	10 (2–22)	11.1 (3.9)		81		11 (3–27)
Bowel diary data
Time spent on toilet (minutes per week)
Baseline	75.6 (69.6)		80	57.5 (3–330)	75.8 (74.4)		87		55.0 (3–370)
Week 6	77.9 (73.3)		66	55.0 (5–315)	85.0 (88.5)		85		50.0 (2–400)
Week 24	78.2 (92.4)		53	45.0 (3–550)	77.0 (68.5)		78		56.5 (1–295)
Number of attempts per week to empty the bowels
Baseline	10.4 (6.7)		86	9 (0–35)	8.6 (5.2)		91		8 (0–32)
Week 6	11.3 (7.1)		65	9 (2–32)	8.9 (6.0)		88		8 (1–32)
Week 24	10.7 (7.2)		53	10 (1–43)	8.3 (5.1)		77		7 (1–23)
Number of stools passed per week
Baseline	3.9 (1.7)		88	4.0 (0–7)	4.0 (1.7)		98		4 (0–7)
Week 6	4.3 (1.9)		68	4.5 (1–7)	3.9 (1.8)		89		3 (0–7)
Week 24	4.3 (1.9)		57	4.0 (0–7)	3.9 (1.9)		81		4 (0–7)
Bladder symptom severity
SF-Qualiveen total bladder scorec
Baseline	1.8 (1.10)		90	1.8 (0–4)	2.0 (1.20)		99		1.8 (0–4)
Week 6	1.7 (1.13)		61	1.6 (0–4)	2.1 (1.15)		85		2.1 (0–4)
Week 24	1.7 (1.10)		57	1.8 (0–4)	2.1 (1.12)		81		2.0 (0–4)
QoL
EQ-5D-5L VAS scored (maximum score of 100)
Baseline	60.6 (21.1)		89	60 (3–100)	55.7 (20.6)		98		60 (3–100)
Week 6	59.4 (24.0)		59	65 (5–97)	55.4 (20.8)		86		60 (5–100)
Week 24	59.8 (22.6)		58	62.5 (10–95)	51.3 (20.3)		83		50 (10–90)
EQ-5D-5L health index scoree (maximum score of 1)
Baseline	0.50 (0.25)		95	0.6 (–0–1)	0.50 (0.28)		99		0.6 (–0–1)
Week 6	0.50 (0.29)		60	0.6 (–0–1)	0.50 (0.27)		84		0.5 (–0–1)
Week 24	0.50 (0.28)		58	0.6 (–0–1)	0.50 (0.28)		83		0.5 (–0–1)
New QoL measure for validation (NBIS)
NBISf (total score maximum of 52)
Baseline	20.2 (8.5)		86	20 (6–41)	20.8 (7.4)		98		21 (5–38)
Week 6	19.9 (8.2)		56	19 (5–42)	21.4 (7.0)		82		21 (3–42)
Week 24	19.0 (8.4)		56	18 (5–50)	20.9 (7.4)		77		21 (1–40)
NBIS QoL (maximum score of 24)
Baseline	9.6 (5.1)		88	9 (0–22)	10.7 (4.7)		99		11 (1–22)
Week 6	9.9 (4.9)		56	10 (0–21)	10.7 (4.3)		83		11 (1–23)
Week 24	9.2 (4.8)		58	8.5 (2–23)	10.7 (4.7)		80		11 (0–24)
NBIS faecal incontinence score (maximum score of 12)
Baseline	3.7 (2.4)		90	3 (0–10)	3.7 (2.0)		99		3 (0–9)
Week 6	3.6 (2.3)		61	3 (0–9)	4.1 (2.1)		87		4 (0–11)
Week 24	3.8 (2.5)		57	4 (0–12)	4.1 (1.8)		82		4 (0–9)
NBIS symptom score (maximum score of 16)
Baseline	6.9 (2.9)		88	7 (0–16)	6.4 (3.1)		98		6 (1–13)
Week 6	6.4 (3.2)		60	6 (1–14)	6.6 (2.5)		84		6 (1–14)
Week 24	6.0 (2.8)		57	6 (1–15)	6.2 (2.8)		80		6 (0–14)

TABLE 5 - Analysis of change from baseline of the NBDS

Adjusted for baseline value, centre, mobility (walking unaided, walking aided or wheelchair bound) and sex. Centre was entered as a random factor.

Time point	Trial group				Mean difference in change between groups (intervention–control), mixed models
	Intervention (N = 90)		Control (N = 99)
	n	Mean change (95% CI)	n	Mean change (95% CI)	Adjusteda (95% CI)	p-value
Baseline to week 6	61	0.6 (–0.73 to 1.98)	80	0.9 (–0.5 to 2.22)	–0.58 (–2.38 to 1.22)	0.5236
Baseline to week 24	66	–0.6 (–2.11 to 0.93)	80	0.5 (–0.78 to 1.83)	–1.64 (–3.32 to 0.04)	0.0558

FIGURE 4.

Change in NBDS over time.

FIGURE 5.

Box-and-whisker plot for NBDS.

Secondary outcomes

Constipation Scoring System

At baseline, the intervention group had a mean CSS score of 11.7 points (SD 4.05 points), and the control group had a mean CSS score of 11.5 points (SD 3.77 points). At week 24, the intervention group had a mean CSS score of 10.1 points (SD 4.10 points), and the control group had a mean CSS score of 11.1 points (SD 3.91 points). Figure 6 is a line graph showing the change over time in the two groups. There was no significant mean difference between the groups in change in the total CSS score between baseline and either time point (Table 6).

FIGURE 6.

Change in total CSS score over time.

TABLE 6 - Analysis of change in CSS score from baseline

Adjusted for baseline value, centre, mobility (walking unaided, walking aided or wheelchair bound) and sex. Centre was used as a random factor.

Time point	Trial group				Mean difference in change between groups, mixed models
	Intervention (N = 90)		Control (N = 99)
	n	Mean change (95% CI)	n	Mean change (95% CI)	Adjusteda (95% CI)	p-value
Baseline to week 6	57	–1.2 (–2.11 to –0.33)	82	–0.3 (–1.05 to 0.48)	–0.89 (–2.03 to 0.26)	0.1273
Baseline to week 24	56	–1.1 (–2.15 to –0.1)	81	–0.3 (–1.08 to 0.45)	–0.88 (–2.03 to 0.27)	0.1308

Short Form Qualiveen Bladder Questionnaire

At baseline, both groups demonstrated moderate effects of bladder dysfunction on their overall quality of life with a total SF-Qualiveen score in the intervention group of 1.8 points (SD 1.10 points) and the control group of 2.0 points (SD 1.20 points). The results in all four domains of the SF-Qualiveen, that is (1) bother with limitations, (2) frequency of limitations, (3) fears and (4) feelings related to urinary problems, were also similar in both groups There were no significant differences between groups in the change from baseline to weeks 6 or 24 in the SF-Qualiveen score (Table 7).

EuroQol-5 Dimensions, five-level version: quality-of-life outcomes

All the results of the EQ-5D-5L are summarised in Chapter 4.

Neurogenic bowel dysfunction patient-reported outcome measure

There were no significant changes in any of the outcomes from the NBIS. All results are summarised in Table 8.

Bowel diary data

Within the statistical analysis plan (SAP), we identified the most important data to be analysed in the bowel diary. These were the number of days passing stools, time spent on the toilet and percentage of normal stools.

Each participant was required to complete 8 weeks of bowel diaries (at baseline, weeks 1–6 and week 24). Overall, these were well completed and compliance was high. For example, frequency of passing of stool was completed by 88 out of 90 (97.7%) participants and 98 out of 99 (98.9%) participants at baseline; by 68 out of 90 (75.5%) and 89 out of 99 (89.8%) participants at 6 weeks; and by 57 out of 90 (63%) and 81 out of 99 (81%) participants at week 24 for the intervention and control groups, respectively.

Stools passed per week

The mean frequency of stools passed per week at baseline was 3.9 (SD 1.68 stools passed per week) in the intervention group and 4.0 (SD 1.74 stools passed per week) in the control group. At week 6, this increased to 4.3 stools passed per week (SD 1.87) in the intervention group and decreased to 3.9 stools passed per week (SD 1.81) in the control group; at week 24, there was no change from week 6 in either group [i.e. mean frequency of stools passed per week was 4.3 (SD 1.88) in the intervention group and 3.9 (SD 1.89) in the control group]. Figure 7 is a line graph visually showing the change over time within the two groups.

FIGURE 7.

Change in the mean number of stools passed per week.

There was a statistically significant difference between trial groups in the change in number of stools passed from baseline to week 24 (Table 9). The difference between the trial groups was 0.62 (95% CI 0.03 to 1.21; p = 0.039). As there was some inconsistency in completion of the diaries, the analyses of change values were derived from a combination of two questions [(1) how often did you pass a stool? and (2) type of stool] to give one answer on frequency. If one or the other question was answered, this was taken as having passed a stool; if neither question was answered, this was taken as no stool passed. Figure 8 highlights very little change in the first 5 weeks.

FIGURE 8.

Box-and-whisker plot of number of stools passed per week.

Time spent on the toilet

At baseline, those in the intervention group spent a mean of 75.6 minutes (SD 69.60 minutes) per week on the toilet and those in the control group spent a mean of 75.8 minutes (SD 74.36 minutes) per week on the toilet. At week 6, this time was 77.9 minutes (SD 73.26 minutes) per week for the intervention group and 85.0 minutes (SD 88.52 minutes) per week for the control group. At week 24, these times were 78.2 minutes (SD 92.43 minutes) and 77.0 minutes (SD 68.51 minutes) per week for the intervention and control groups, respectively. There was no statistically significant difference between groups in the mean change in time spent going to the toilet between baseline and either time point (Table 10).

Type of stool

For each stool passed, participants were asked to indicate the type of the stool, as per the Bristol stool chart. 33 Using types 3 and 4 as normal, and types 1 and 2 and no stool per week as constipated, there was a reduction in the percentage of participants who were constipated in the intervention group (from 61.6% at baseline to 55.4% at week 24) and in the control group (from 59.0% to 58.9% at week 24). The percentage passing normal stools (types 3 and 4) was 20.2% in the intervention group and 17.5% in the control group at baseline; at week 24 this percentage was 23.9% in the intervention group and 22.8% in the control group (see Appendix 5).

Medications used in the AMBER trial for bowel management (information from medication form)

At baseline, 67 (74%) participants in the intervention group and 80 (80%) participants in the control group were on at least one medication, with numbers of medications ranging from 1 to 35. The number of participants on medication for management of their bowel symptoms was 44 (i.e. 44/67; 66%) in the intervention group and 54 (i.e. 54/80; 68%) in the control group. Laxido Orange (Almac Pharma Services Ltd, Craigavon, UK), Movicol (Norgrine Ltd, Hengoed, UK) and docusate sodium appeared to be the most popular medications used in both groups, with suppositories being used by approximately only 9% of participants in each group.

At the start of the trial, 44 participants were on zero medications (24 participants in the intervention group and 20 in the control group).

During the course of the study, 32 participants in the intervention group and 44 participants in the control group started new medications, with nearly twice as many new medication entries recorded in the control group compared with the intervention group (69 vs. 135). Thirteen participants in the intervention group had taken at least one additional medication for bowel management, with 19 different entries recorded in total (e.g. one participant had five entries for four different laxatives). In the control group, 12 participants started new medications for their bowels, with 33 different entries (several participants reported three or four additional bowel medications; one had 12 entries, eight for different bowel medications and four for glycerine suppositories).

At the end of the study, 15 participants in the intervention group (18 entries in total) and 13 participants in the control group (35 entries) had stopped taking some of their bowel management medications. There were still 38 participants who were not on any form of medication (intervention group, n = 20; control group, n = 18) at the end of the study.

Anorectal physiology and transit test results

University College Hospital, London, was the only site in the AMBER trial to recruit participants to a pilot substudy, to determine if any information about the mechanism of action of abdominal massage could be gleaned through anorectal physiology and colonic transit tests, which are routinely undertaken at this site. Participants had a test at baseline and a repeat test at week 24. All participants from UCH took part in the substudy.

A total of 26 participants were randomised at UCH; however, two post-randomisation exclusions occurred. All baseline outcomes for the main study were completed by 24 participants. Of these, 23 participants underwent baseline transit tests; the 23 participants comprised two male (8.7%) and 21 female (91.3%) participants, 11 from the intervention group and 12 from the control group, with a mean age of 53.5 years (SD 12.59 years). There were no baseline transit test data for one of the 24 participants. Three participants withdrew from the study during the 6 weeks of intervention and a further participant was lost to follow-up (could not be contacted for the week-24 follow-up and did not return any patient-reported outcomes). A further eight participants withdrew from having the repeat tests at week 24, leaving 12 participants with week-24 transit and physiology results. One of these participants had no baseline transit data; thus, 11 sets of baseline and week 24 transit test data were available for analysis.

There was no difference between the groups with respect to changes in the duration of bowel symptoms, faecal incontinence, infrequent emptying, pain or bloating (see Report Supplementary Material 1). The baseline data indicated that 65.2% (15/23) of the participants who underwent the transit test had slow transit, six (54.5%) in the intervention group and nine (75%) in the control group.

Table 11 shows that there was no significant difference in the change in the number of total markers between the groups; although there was a possibility that the groups were not well matched at baseline with a median number of markers of 17 (range 0–54) in the intervention group, while in the control group the median number of markers was 47 (range 0–60). The CI is wide because of the small number of participants. The markers in the rectosigmoid were relatively well matched at baseline, median 10 (range 0–46) in the intervention group and a median 12.5 (range 0–35) in the control group.

Notwithstanding the substantial number of participants who failed to complete the test at week 24 (five in the intervention group and six in the control group), the change between pre treatment and week 24 was 16 (range –6 to 32) in the intervention group and –5.0 (range –13 to 17) in the control group. This may be explained by the fact that, in the intervention group, the massage was moving content to the distal colon, if not necessarily triggering evacuation.

The difference at baseline for the total markers and markers in the left and right colon, that is, groups not matched at baseline for these outcomes, as well as the numbers not completing the test at week 24, make it impossible to differentiate between changes as a result of regression to the mean and actual changes.

Anorectal pressure tests and anal and rectal sensation and capacity

The small number of participants who completed the tests at week 24 mean that the sample size is too small to draw conclusions.

Adverse events

A total of 84 AEs were noted in the trial: 28 in the intervention group and 56 in the control group. Table 12 summarises this information, along with the numbers of participants affected in each group.

Appendix 6 is a summary of all the AEs. Five AEs were reported as being possibly related to the intervention; however, two of these were reported in the control group [urinary tract infection (UTI) and diarrhoea]; as they had no intervention, the fact that there were two AEs in this group that were classed as possibly related to the intervention is deemed as an error on the part of the site reporting the AE. For the three possibly related AEs reported in the intervention group, two were for one participant who had two UTIs, both of which resolved within 1 week, and one participant had reflux and went to accident and emergency (A&E) but was not admitted. Both of these participants were still continuing with the massage at 24 weeks despite these reported AEs.

Additional information on all AEs (reported by primary SOC and PT) can be found in Report Supplementary Material 1.

Summary of serious adverse events

From the 84 reported AEs, nine were classified as a SAE. A summary of the SAEs reported is in Appendix 6. Two of these SAEs were a hospitalisation as a result of a MS relapse (one in each study group) and one was a fall, but, considering the study cohort, these are not surprising events. None was related to the trial and all were resolved.

Secondary analysis

In a secondary analysis of the primary outcome, using MI for the missing data, the following baseline variables were included in the model: age, sex, BMI, type of MS, number of years since diagnosis, cognitive symptoms of MS and minimisation variable level of mobility (walking unaided, walking aided or wheelchair bound). Table 13 shows the results adjusted for all variables; this indicated a similar result as found in the primary analysis, with no significant difference between the intervention and control groups. For assessing if changes in symptoms were dependent on site, with Edinburgh taken as the reference site, there was no statistically significant difference between the sites (p = 0.8326), although slightly better results were reported at sites in Sheffield, Salford, Lincoln, Leeds and the John Radcliffe Hospital than in Edinburgh. Regression analysis also indicated that there is more likely to be a benefit in the intervention group for those walking unaided or aided, as they responded better than wheelchair-bound participants, while those of greater age and higher BMI also did slightly better. The time since diagnosis of MS did not seem to be important, but those with relapsing–remitting MS responded more positively than those with primary progressive MS. Cognition severity indicated that those with mild or no impairment did better than those with severe impairment. Consistent with other findings, males responded significantly better (mean difference –2.789, 95% CI –5.179 to –0.399; p = 0.0226).

Sensitivity analysis

A sensitivity analysis was carried out using MI of the primary outcome NBDS, and a similar result to the primary analysis was found (difference in change between the intervention and control group: –1.266, 95% CI –2.936 to 0.403; p = 0.1371) (Table 14). Males, however, again demonstrated a greater beneficial effect (males vs. females: –2.280, 95% CI –4.478 to –0.083; p = 0.0419).

The repeated-measures analysis (Table 15) was not significant for the primary outcome or all other outcomes, except for the increased number of times that participants felt that their bowel was emptied and the number of stools passed per week, which were in favour of the intervention. Between baseline and week 6, the mean difference in the number of stools for the intervention group was 0.98 (95% CI 0.36 to 1.61; p = 0.03902) and for the control group it was 0.56 (95% CI 0.03 to 1.10; p = 0.039). This effect was decreased for both outcomes at week 24, but was still statistically significant over all time periods.

Change in laxative use

At week 6, the outcome for the regular use of laxatives or drops at week 6 compared with no use of laxatives or drops had an odds ratio (OR) of 2.37 (95% CI 0.87 to 6.46; p = 0.092), using ordinal regression adjusted for all baseline variables (baseline use, centre, age, sex, mobility, BMI, time since diagnosis of MS, type of MS and cognitive status). At week 24, the OR for the same outcome was 1.62 (95% CI 0.74 to 3.55; p = 0.229) using ordinal regression adjusted for all the same baseline variables. Although the ORs were not significant, there is some evidence that the intervention group were twice as likely to achieve a lower level of laxative use than the control group (Table 16).

Post hoc analysis

The following descriptive analysis (and, when indicated, further statistical analysis) focuses on questions within questionnaires and on further bowel diary data on symptoms that were identified as being important to participants and/or were identified in other analyses as significantly changed between the two groups.

Neurogenic Bowel Dysfunction Score: those with constipation at baseline (i.e. with a score of ≥ 11 points)

As the overall level of constipation at baseline was rated as mild in both groups according to the NBDS [at baseline the total mean score for the intervention group was 7.6 points (SD 5.31 points) and the median was 6.0 points (range 0–21 points), whereas in the control group, the mean was 8.6 points (SD 5.08 points) and the median was 9.0 points (range 0–22 points)], the analysis was repeated for only those participants with a NBDS at baseline of ≥ 11 points. The results are presented in Table 17.

The univariate analysis and linear regression analysis can be reviewed in Report Supplementary Material 1. The numbers in both groups were reduced and the only evidence of any effect was at week 6 for those with a longer time since diagnosis of MS (F_4,30, p = 0.043, estimate 0.153, t-test value 2.07, p = 0.0437, 95% CI 0.004 to 0.302).

Frequency of defaecation as per question 1 in the Neurogenic Bowel Dysfunction Score

There was an increase in the number of participants passing stools daily from baseline to week 24 in the intervention group (12.2% to 23.6%), with a smaller increase in the control group (16.2% to 20.0%). The intervention group had a small decrease in the percentage passing stools fewer times than once per week (6.7% to 5.6%), compared with an increase in the control group (7.1% to 12.2%).

Frequency of defaecation as per the question in the Constipation Scoring System

The percentage of participants in the intervention group who were passing stool two or more times per week by week 6 was 92.1% and in the control group it was 88.6%; at week 6, 6.6% in the intervention group and 10.1% in the control group were passing stool fewer times than once a week. At week 24, the percentage of participants passing stools more than two times per week had increased to 94.9% in the intervention group and had decreased in the control group to 80.7%; 3.4% of the intervention group were now passing stools fewer times than once per week, whereas in the control group this percentage had increased to 16.8%.

Feeling of incomplete evacuation as per the question in the Constipation Scoring System

At baseline, the percentage of participants who ‘never felt incomplete evacuation’ was 6.7% in the intervention group and 9.1% in the control group; at week 24, this increased to 15.5% in the intervention group and decreased to 8.4% in the control group. At baseline, 21.3% of participants in the intervention group and 20.3% in the control group ‘always felt incomplete evacuation’; at week 24 this decreased to 3.4% in the intervention group and 10.8% in the control group.

Bowel diary data

Attempts to pass stool

At baseline, the mean number of attempts to pass stool in the intervention group was 10.4 (SD 6.73 attempts), whereas for the control group this mean was 8.6 (SD 5.22 attempts). At week 6, the mean number of attempts was 11.3 (SD 7.31 attempts) for the intervention group and 8.9 (SD 6.00 attempts) for the control group; and at week 24 the mean number of attempts to pass stool was 10.7 (SD 7.16 attempts) and 8.3 (SD 5.09 attempts) for the intervention and control groups, respectively.

As can be seen in Table 18 and Figure 9, the mean changes between baseline and weeks 6 and 24 for attempts to empty the bowel were not statistically significant between groups.

TABLE 18 - Attempts to pass stool per week

Adjusted for baseline value, centre, mobility (walking unaided, walking aided or wheelchair bound) and sex. Centre was used as a random factor.

Time point	Trial group				Mean difference in change between groups, mixed models
	Intervention (N = 90)		Control (N = 99)
	n	Mean change from baseline (95% CI)	n	Mean change from baseline (95% CI)	Adjusteda (95% CI)	p-value
6 weeks	62	0.2 (–1.49 to 1.84)	84	0.4 (–0.83 to 1.66)	1.08 (–0.81 to 2.96)	0.2608
24 weeks	52	–0.9 (–2.82 to 1.02)	75	–0.5 (–1.96 to 1.0)	1.14 (–0.92 to 3.19)	0.2770

FIGURE 9.

Frequency of feeling of successful evacuation.

At baseline, the number of times per week that the participants felt that they had a complete evacuation was 1.9 (SD 2.2 times) and 1.8 (SD 1.73 times) for the intervention and control groups, respectively. At week 6, this was 2.6 times (SD 2.2 times) and 2.2 times (SD 2.0 times) for the intervention and control groups, respectively, and at week 24 this number was 3.0 times (SD 2.16) and 2.2 times (SD 2.14 times) for the intervention and control groups, respectively.

There was a statistically significant difference between groups in the change in number of complete evacuations per week from baseline to week 24 (p = 0.002) (Table 19). The intervention group had, on average, increased the number of complete evacuations per week by 1.08 more than the control group, although this was a post hoc analysis.

TABLE 19 - Number of times a complete evacuation per week was reported

Adjusted for baseline value, centre, mobility (walking unaided, walking aided or wheelchair bound) and sex. Centre was used as a random factor.

Time point	Trial group				Mean difference in change between groups, mixed models
	Intervention (N = 90)		Control (N = 99)
	n	Mean change from baseline (95% CI)	n	Mean change from baseline (95% CI)	Adjusteda (95% CI)	p-value
6 weeks	62	0.8 (0.4 to 1.2)	84	0.2 (–0.2 to 0.6)	0.48 (–0.10 to 1.06)	0.104
24 weeks	52	1.2 (0.6 to 1.8)	75	0.3 (–0.1 to 0.7)	1.08 (0.41 to 1.76)	0.002

Other diary data

Analysis of other data provided by the self-completed bowel diary was not statistically tested as per the SAP (e.g. frequency of faecal incontinence, use of digital stimulation, type of stool) and no change was identified between groups to warrant post hoc analysis. The bowel diary question on laxative use asked if laxative use was the same, less or more. This was difficult to analyse as it was not being compared with baseline but with the previous week.

Adherence to the intervention (massage diary and nurse weekly telephone calls)

All participants received weekly telephone calls from the research nurse during the 6 weeks of intervention and again at week 24. The aim of the calls was to support fidelity to the trial protocol. There was good response to the follow-up telephone calls made by research staff at sites; 81% of participants in the intervention group and 86% in the control group were reached at week 24 and data were collected during the telephone calls.

According to information collected during the follow-up calls, 72.6% to 83.3% of participants in the intervention group administered the massage themselves throughout the 6 weeks of intervention; for 10.3% to 14.1% of participants, a carer undertook the massage. Some data were missing or massage was not undertaken in 2.6% of cases.

According to the bowel diary records, which also recorded when the massage was undertaken in the intervention group, the mean number of days on which massage was performed per week was 5.2 (SD 1.88). This varied little over the 6 weeks of intervention [at week 6, the mean was 5.4 days (SD 1.75)]. At week 24 those still doing the massage (n = 57, 82%) were undertaking it on average 3.2 times per week (SD 2.83 times per week). Mean time spent on the massage during weeks 1–6 was 72.5 minutes (SD 4.0 minutes) and at week 24 it was 55.8 minutes (SD 40.0 minutes).

Participants were shown how to perform the massage lying down, semi-lying down or sitting up. Information on the choice of position utilised, in addition to the time of day the massage was performed, was collected during the 6 weeks of the intervention. During weeks 1–6, 58–64% of participants performed the massage lying down, 16–24% semi-lying down and 1–4% sitting up.

Morning massage administration seemed to be the preferred time (for 46–56% of all participants), then evening (26–31%), with afternoon administration being least common (4–6%).

Information from nurse weekly telephone calls

Reasons for discontinuing the intervention, as reported in the final week 24 telephone call with the research nurse (n = 77 interviews; 20 discontinued), included no benefit (n = 8; 10%), burden on carer (n = 1; 1.3%) and too difficult (n = 5; 6.5%); the rest gave no reason or data were missing.

Neurogenic bowel impact score

Analysis of the new NBD symptom score was undertaken for further validation; the analysis carried out is in Report Supplementary Material 1.

The new neurogenic bowel patient-reported outcome measure (NBIS) showed only moderate repeatability in the control group for the AMBER trial. However, this was over a longer time period than is usually used for test–retest stability, and it is possible that the MS bowel symptoms had genuinely changed in the control group. It is known that MS bowel symptoms are variable over time. A repeat of this test–retest with a shorter time between the completions, and possibly asking participants if they perceive that their symptoms changed or not, is recommended.

When compared against other bowel symptom scores, such as the NBDS and the Wexner score, a high correlation was found for most items, suggesting good criterion validity for the new questionnaire. It was also highly correlated with the EuroQol-5 Dimensions (EQ-5D) quality-of-life score, but not the EuroQol Visual Analogue Scale (EQ-VAS). NBIS was strongly correlated with the primary outcome measure NBDS. As the new questionnaire was developed after extensive qualitative work with people with NBD, including those with MS, this lends credibility to both scores. However, neither score showed a significant difference between our intervention and control groups, so there is no evidence that one is more responsive to change that the other. Further work is needed to determine which score patients find better reflects what is important to them. As our trial found no significant difference between groups, we are not able to recommend either score as being more or less sensitive to change. We did not find anything to suggest an advantage to either questionnaire and both had similar completion rates.

However, some questions within the NBDS (primary outcome) were difficult for some patients to fully understand (e.g. digital stimulation, use of drops), whereas in the new questionnaire, the language was better but the whole questionnaire was felt to be too long.

Economic evaluation

The aim of the AMBER trial was to determine the clinical effectiveness and cost-effectiveness of abdominal massage (intervention) as part of an adjunct to the control of optimised bowel care in PwMS who have NBD. This chapter gives the results of a formal economic evaluation of the AMBER trial intervention compared with control from a NHS and patient cost perspective. Health-related quality-of-life (HRQoL) data and health-care resource-use data were used to examine the following:

• the cost of delivery for the patient groups

• the health-care costs for participants in both trial groups

• HRQoL through calculation of utility values using the EQ-5D-5L.

Using the above information, we calculated an incremental cost-effectiveness ratio (ICER) and the probability of the intervention being cost-effective at different thresholds of willingness to pay (WTP) per QALY gained.

Data related to the economic analysis

EuroQol-5 Dimensions, five-level version, data

The EQ-5D-5L data were collected via participant-completed questionnaires at baseline, week 6 and week 24. The EQ-5D-5L responses were given in the two sections of the EQ-5D-5L questionnaire: the EQ-VAS and the EQ-5D Descriptive System. 43 The EQ-5D-5L Descriptive System was scored using the UK tariffs. 44 Table 4 provides a summary of the EQ-VAS and EQ-5D Descriptive System index score. Higher scores represent better quality of life. In the cost-effectiveness analysis that follows, HRQoL, as measured by the EQ-5D-5L index scores in Table 4, is combined with resource-use costs as shown in Appendix 8 and intervention costs (which were described in Abdominal massage costs and calculated as £90), and assigned to each participant in the intervention group.

Economic evaluation of abdominal massage (intervention) versus standard care (control)

The raw data indicate that there is little difference between the two groups in this trial both in HRQoL outcomes and costs. However, there were fewer quality-of-life data to analyse than the number of recorded participant withdrawals or losses to follow-up. Missing data occur frequently in RCTs as participants may withdraw, questionnaires may be unreturned and responses to individual questionnaire items may be impossible to use. In the AMBER trial, one reason for the differing numbers was the fact that, in some instances when missing outcome data were chased, participants said that they had already completed the outcomes and returned them by post, but these were never received (previously discussed in Chapter 3).

At the end of the trial, 58 participants in the intervention group and 83 participants in the control group had EQ-5D-5L data to analyse. To account for the missing data, and the highly imbalanced nature of the two groups that resulted in more missing values in the intervention group, the following statistical approaches45 were used: EQ-5D-5L data were analysed (Table 22) and then MI was performed. The imputed data sets were then bootstrapped to perform a cost-effectiveness analysis including NHS resource-use costs and interventions costs. In the economic evaluation that follows, NHS resource use included all costs related to both bowel issues and other health issues as reported in Appendix 9.

The results in Table 22 are not adjusted for missing values. The economic analysis of the AMBER trial data employed methods described in another study to handle missing data by MI (to reduce bias and ensure that missing data are handled appropriately). 46 The economic evaluation, therefore, also included participants with only partial data. For the cost-effectiveness analysis, QALYs and total patient costs were calculated for the 6 months that the trial lasted. The imputation was run 60 times, resulting in 60 different data sets to be used in the cost-effectiveness analysis. The imputation was implemented separately for the intervention and control groups to account for differences in the missing values between the two groups.

Multiple imputation was performed using predictive mean matching. 47 The MI model uses baseline covariates (EQ-5D index scores, age, sex, time since diagnosis of MS and severity of MS symptoms), costs and QALYs at each follow-up to impute unobserved costs and QALYs, so that, for example, missing costs at week 24 are imputed using data on baseline covariates, costs at baseline and week 6 (if available) and QALYs between baseline and week 6 (if available). QALYs were imputed using EQ-5D index scores. One thousand bootstrap samples were drawn from each of the 60 multiply imputed data sets, analysed and the difference in net benefit between the treatment groups in each bootstrap sample was estimated (at a given threshold for cost per QALY). The proportion of bootstrap samples in which the net benefit is positive represents the probability that the treatment is cost-effective for each multiply imputed data set. This probability is then averaged across all multiply imputed data sets.

Tables 23 and 24 show resource-use spending at 24 weeks before and after imputation. As expected, resource use remains not statistically significantly different between the two groups after imputation. Table 25 shows the estimates of costs and QALYs per patient in the MI models. These costs include intervention costs and resource-use costs as shown in Table 25. QALYs were calculated from EQ-5D index score, taking into account the fact that the trial lasted only 6 months.

Table 26 shows the average incremental costs and QALYs for every participant obtained from the multiply imputed sample and the bootstrapping. The ICER based on these data is negative at –£24,149 because the model estimates a negative incremental QALY.

This method accounts for the uncertainty around the mean estimates of both costs and QALYs; to make conclusions about the cost-effectiveness of abdominal massage compared with control, the probability of cost-effectiveness at the WTP threshold of £20,000 per QALY is calculated at 31.3%. That probability increases to 34.2% for a WTP threshold of £30,000 per QALY.

To test if the results were affected by the imputation or the bootstrapping processes, two extra models were estimated. First, it was estimated that a seemingly unrelated regression model was applied on the imputed data sets. 48 Second, a mixed model was employed using maximum likelihood estimation. 44,49 The mixed model did not require an imputation step; this approach is a good check to see if imputation affected the results. The results of the seemingly unrelated regression model and the mixed model are shown in Appendix 7.

These results are similar to the bootstrapping model, and all three methods predict a probability of cost-effectiveness that is < 50% at the WTP threshold of £20,000 per QALY gained. Both imputation models predict a negative QALY gain after controlling for baseline HRQoL in these models. For this reason, the ICER of these models is negative, making straightforward comparisons rather difficult. The mixed model also controlled for baseline HRQoL but the estimate on incremental QALYs and the ICER of this model was positive. In all three estimated models, the impact on quality of life is close to zero, with relatively large standard errors reflecting the uncertainty around patient utility scores. The mixed-model point estimate of the ICER is at £28,722, which is over the £20,000 WTP threshold.

In sensitivity testing, patient characteristics (age, sex, time since diagnosis of MS and severity of MS symptoms) were further controlled for, along with baseline HRQoL, in the three models, but this did not significantly change the results. In another sensitivity test, unit costs were varied by 20%, but this did not have a significant impact on the probability of cost-effectiveness, possibly because of similar resource use between the two groups. In a final sensitivity test, the impact of changing the intervention cost was explored. All three models were ran with the intervention halved and doubled. The results do appear sensitive to the intervention cost, as the probability of cost-effectiveness at the WTP threshold of £20,000 per QALY gained ranges from 21% for high intervention costs of £180 per patient to 55% probability of cost-effectiveness for low costs of £45 per patient. Notably, the point estimate of the ICER drops to between £6000 and £7000, which is in the cost-effective range given a WTP threshold of £20,000 per QALY gained. As described earlier, it is more likely that the intervention costs will be < £90 per patient than > £90, and the results in Appendix 7 should be considered as conservative. However, it should be noted that given the negative QALY increment, the control was bound to dominate as long as the mean cost was higher in the intervention group.

The economic evaluation results show that abdominal massage is less likely to be a cost-effective alternative to standard care than the other way around. However, all models predicted a probability of cost-effectiveness of > 30% and, in the mixed model, close to 47%. In the sensitivity analysis, this probability was > 55% assuming a low intervention cost per participant. The probability of cost-effectiveness can be seen as the probability that an individual (random) patient will have a positive individual incremental net benefit. It can also be seen as the proportion of all patients in the population who have positive individual incremental net benefits; therefore, it is reasonable to assume that our results suggest that there is a subset of patients who had a positive incremental net benefit from abdominal massage. 50 If there were no patients with a positive net incremental benefit, then the likelihood of cost-effectiveness would have been close to zero. Further research is needed to establish the type of patient that may have benefited from abdominal massage (discussed further in Chapter 6).

This economic evaluation has certain limitations. First, excluded drug costs and out-of-pocket costs were excluded because very few participants responded to these questions. The participants who responded reported very low costs per patient and it is not expected that inclusion of these would have a large impact on our results. Second, subgroup analysis, by estimating these models on a subset of participants, was not performed. This was decided against because regression results (available on request) did not show a statistically significant impact of participant characteristics, such as age and sex, on costs and QALYs gained. Finally, the results were not extrapolated over a horizon longer than 6 months. The results suggest that the impact of the intervention on quality of life as measured by the EQ-5D-5L is small and significant differences in the probability of cost-effectiveness are not expected if the trial lasted for a longer period.

Introduction

The AMBER trial included a process evaluation, in line with advice from the Medical Research Council guidance for evaluating complex interventions. 51,52 This was informed by realist evaluation methodology, which goes beyond the evaluation question ‘What works?’ to ‘What works, for whom and in what context?’53 The aim of this approach is to situate and explain outcomes within the contexts in which they are achieved in order to explain potential discrepancies between expected and observed outcomes, and to assess fidelity to implementation processes. Furthermore, results of the process evaluation also provide data to inform the optimisation of the intervention and seek to explore potential routes to sustainable implementation. The process evaluation follows a longitudinal case study design. 54,55

The objectives of the process evaluation are to explore:

• fidelity to processes of implementation of the trial intervention

• implementation contexts (including settings, demographics and implementation processes, delivery and take up of the intervention, and adherence and non-completion)

• intervention optimisation and sustainability beyond the life of the funded project.

This chapter presents the research methods for the process evaluation, the results of the analysis of data from interviews, bowel diaries and telephone support recordings. The chapter ends with practice recommendations.

Methods

Recruitment and sampling

People with multiple sclerosis

A total of 20 PwMS taking part in the trial, and randomised to the intervention group, were selected via convenience sampling. 56 The small numbers recruited into the trial from each site meant that our intended purposive sampling strategy was not feasible. However, as Figure 1 illustrates, the sample achieved a variation in terms of geographical location, age, MS type and different stages of the disease progression. This sample variation facilitated the exploration of hypothesised context–mechanism–outcome (CMO) configurations. We did not adhere rigidly to definitions of ‘contexts’ or ‘mechanisms,’ since previous experience of using this approach informed us that contexts can become active mechanisms that promote change in some instances and, at other times, mechanisms of action can be better conceptualised as contexts. 57,58 For instance, sampling reflected the following hypotheses: that there could be sex differences in the acceptability of massage, severity of MS might have an impact on ability to do the massage and length of time living with MS may also contribute to attitudes towards self-care. This sample is reflective of the characteristics of trial participants as a whole, with those aged > 50 years and women being the most prominent. The mean age for the intervention group participants was 52.2 years (51.3 years for those in the control group); 84.4% of intervention participants were female (78.8% for the control group). Of the interview participants, 16 lived in the north of England, reflecting the fact that half of the 12 sites involved in the study were located in that part of the UK. Table 27 provides further details on the characteristics of those interviewed. Figure 10 shows the flow chart for the process evaluation.

TABLE 27 - Characteristics of interviewed participants

This is estimated, as a number of participants reported living with MS symptoms for years.

Characteristic	Number of participants
Age range (years)
< 21	0
21–30	0
31–40	1
41–50	4
51–60	7
> 60	8
Sex
Male	1
Female	19
Employment status
Unemployed	2
Employed	3
Business owner	1
Retired (on ill-health basis)	12
Retired (reached retirement age)	2
Geographical location
West Scotland	3
North-west England	10
North-east England	6
South-east England	1
Type of MS
Benign	0
Relapsing–remitting	11
Secondary progressive	8
Primary progressive	1
Years with MSa
< 5	3
5–10	3
11–20	6
21–30	3
> 30	6

FIGURE 10.

Flow chart for the process evaluation.

By the time of the first interview, participants had been enrolled in the trial for ≈4 weeks. All those who took part in a first interview agreed to participate in a second interview. A total of 20 PwMS were interviewed twice, giving a total of 40 interviews.

Health-care professionals

Forty-two interviews were conducted with 25 different HCPs. One or two people involved in delivering the AMBER trial from each of the 12 sites were recruited to interviews. The range of involvement in the trial varied from those who delivered the massage training and/or the participant follow-up to the local principal investigators, whose role centred on identifying suitable patients for the trial. Appendix 10 documents the roles of the HCPs interviewed and the number of interviews. This sample was also designed to reflect the realist evaluation approach.

Initial interviews with HCPs were usually conducted within a few weeks of recruiting their first intervention participant. Owing to variation in site initiation and trial recruitment, initial interviews took place between January 2015 and March 2016. During this first stage, 23 staff members were interviewed.

Second interviews were sought with staff members who were actively involved in patient training and follow-up, in order to explore any problems that may have arisen since the first stage of interviewing. In a small number of cases, a different staff member who had since become more involved in the trial or delivery of the treatment was selected for interview at the second stage. Nineteen staff members were interviewed in the second stage of interviews.

Stakeholders

Six interviews were carried out with stakeholders purposefully selected for their expertise in neurological and incontinence treatment provision, policy-making and service development. The process of identifying suitable interviewees began with research into neurological and incontinence services throughout the UK. Snowball sampling was also used, meaning those interviewed recommended other potential interviewees. Appendix 10 illustrates the types of organisations that stakeholders came from and the number of interviews.

Fifteen potential interviewees were contacted and six people were interviewed after giving informed consent. The interviews took place from early to mid-2016, in order to capture their knowledge and insights into recent policy and clinical developments related to the treatment of MS.

Data collection

Data analysis

Interview recordings were transcribed verbatim. Data were analysed by drawing on an adapted framework approach. 60 This followed an initial categorising and coding process similar to thematic analysis, using the qualitative data analysis software NVivo version 10 (QSR International, Warrington, UK). Coding and all further stages of analysis were conducted by Selina Doran (SD) and checked for consistency by Fiona Harris (FH). Analysis was conducted continuously with interviewing, contributing to the iterative process, allowing emerging themes of interest to be explored further in future interviews. The initial coding was then transferred into framework matrices for the three categories of interviewees. These summary tables explored within-case issues, in which each trial site was considered as a case, that is, the unit for analysis. During the analysis, attention was paid to any contextual differences that could have an impact on outcomes. Cross-case comparison then identified higher-level themes that explored facilitating contexts and mechanisms, and any barriers to successful implementation. The matrices also tracked the process of change over time, taking account of the longitudinal aspect of interviews. Interviews with PwMS also retained attention to case study sites to ensure that analyses were sensitive to any contextual variations. However, given the small numbers recruited from each site, participants have not been identified by recruitment location. Identifiers in quotes simply read as, for example, PwMS1 or HCP1. When second interviews were conducted with the same person, the identifier illustrates this by the additional number so that, for instance, the second interview with PwMS 1 would be identified as PwMS1_2. Bowel diaries were also analysed for those participants who reported either no improvement or only a temporary improvement in bowel symptoms. To ensure validity and reliability of the analyses, these tables were deliberated within the process evaluation team (SD and FH), and received further clinical input from the wider study team.

Results

This section presents the analysis of interviews with trial participants alongside bowel diary analysis, and analysis of interviews with HCPs and higher-level stakeholders. The within-case descriptive data informed the beginning of Chapter 5; here the focus is on presenting experiences of trial participation and a cross-case comparison of implementation issues drawn from interviews with HCPs.

Contextualising the trial primary outcome

One further piece of analysis was conducted in order to explore the discrepancy between the statistical analysis of the NBD total score and self-reported outcomes of the trial. The NBD total scores for all interviewees were matched up with data from interviews. Table 31 illustrates the discrepancies found by comparing these data. Although 15 interviewees reported some improvements related to the massage, only seven participants recorded an improved NBD score between baseline and week 24, six participants showed no change and seven worsened over the course of the trial. However, of those seven participants who showed improved NBDSs, two of these interviewees self-reported as not having experienced any improvement in their symptoms. There are several potential explanations for these discrepancies. First, both the interview and the NBDS questionnaire captured snapshots of participant experience tied into particular weeks. Although interviews roughly followed the same time point as the trial measures, they were within the same month rather than completed at the same time as the trial measures. Second, and perhaps more importantly, the NBDS questionnaire did not necessarily explore those aspects of participant experience that affected quality of life more generally, hence the discrepancy between self-reported outcomes and those measured by the NBD questionnaire.

Post-trial intentions

From discussions with participants during second-stage interviews, it appeared that all but two of them intended to continue with the massage. This is either because it worked for them or they hoped that it would work in the future. The massage seemed to have been incorporated seamlessly into their routines.

Views on potential future implementation

This section explores the views of both HCPs and stakeholders regarding the potential to implement the intervention within the NHS. These data are situated within the larger body of work conducted by the process evaluation team, and interviews were done on the premise that the intervention may demonstrate effectiveness and were carried out before the results of the trial were known.

Health-care professionals in the majority of sites reported issues related to staff capacity, which represents a potential barrier to future implementation of abdominal self-massage within the NHS.

Across all services in NHS England and Scotland, there are threats to the specialist nurse role and other positions through despecialisation, redundancy and not replacing staff members when they leave. At one site, there was a problem with staff recruitment and retention, which resulted in a reliance on agency staff to deliver the service.

To successfully implement abdominal massage as a form of treatment, staff members would require reassurance regarding workload and capacity. There was a perception that this would require additional resources, although in many cases this might replace more invasive, time-consuming treatments and could reduce the ‘revolving door’ of hospital admission or attendance for severe constipation. There were also concerns that if massage training was extended to other patient groups, there could be a resulting marked increase in referrals:

We could potentially be inundated with patients.

HCP16_2

There was also some debate about which staff members would be best placed to deliver the massage training. It was suggested that massage training could be offered by the colorectal and continence team in hospitals, or built into existing MS or continence clinics. This could be coupled with the DVD and written training materials to assist people in learning the technique. Furthermore, it was suggested that the massage could possibly benefit patients on bed rest or in nursing homes:

That could be something we teach them, to look after more progressive patients.

HCP18_2

It was suggested by some sites that community and district nurses could become involved in training people in massage in their homes. Indeed, there were indications that abdominal massage could be introduced to a wider population in a range of health-care and community settings.

Enthusiasm for abdominal massage was such that a number of sites indicated a willingness to incorporate it into current services. For instance, a HCP from one site who had set up a bowel clinic during the trial said that, since the staff members who delivered the AMBER trial were already trained in the massage, this could be rolled out more widely. Interest was also expressed in distributing training materials and engaging in additional training.

Stakeholders indicated that there are a number of policy and capacity issues affecting the potential for abdominal massage to be successfully implemented within the NHS. Evidence of clinical effectiveness is required in order to convince commissioners and other services to support this new treatment option. Moreover, in the current NHS environment, health boards and trusts are ‘just looking for a short-term gain from cost savings’ (Stakeholder 6), thus evidence of cost-effectiveness is also important.

The case for abdominal massage needs to be persuasive to convince Clinical Commissioning Groups, HCPs and other services to adopt this intervention if it was found to be clinically effective. This might highlight, for instance, the potential for abdominal massage to free up capacity within GP, continence and MS services by dealing with bowel problems before they deteriorate (Stakeholder 4 and Stakeholder 5). Training in the massage could be framed as upskilling staff members:

It should be career-enhancing rather than career-threatening for those involved.

Stakeholder 6

It could also reduce the costs and capacity issues associated with long-term bowel damage: unplanned hospital admissions, bed occupancy and the prescribing of medications/other forms of treatment (Stakeholder 1, Stakeholder 2 and Stakeholder 6). Secondly, there would be the potential to improve quality of life for patients:

It’s the cost to the patient of the indignity of having bowel management such as a suppository.

Stakeholder 2

A potential barrier to implementation is the challenge of ‘getting something from best practice to common practice’ (Stakeholder 4). First, massage treatment would probably be most useful if administered at an early stage in the development of constipation problems, rather than when patients are at crisis point (Stakeholder 3). GPs are integral to this process:

They see the whole person and spot potential issues around bowel dysfunction at a much earlier stage.

Stakeholder 6

A health-care assessment for each individual needs to be carried out to determine what is causing the constipation and to ensure that abdominal massage is the right treatment for them (Stakeholder 2). Furthermore, one stakeholder suggested that abdominal massage should be part of an individual’s self-management programme, supplemented by advice around fluid intake, changes to diet and exercise suggestions (Stakeholder 5). The use of tracking tools like bowel diaries can help demonstrate how things have progressed (Stakeholder 2 and Stakeholder 3).

Stakeholders felt that abdominal massage could be taught by community nurses or other HCPs, such as general nurses, physiotherapists and continence advisors (Stakeholder 3). They also suggested that consideration should be given as to how this treatment could be taught to those who are severely disabled and unlikely to be able to self-massage (e.g. those in care homes). As reported by HCPs above, this suggests the need for staff members at care homes to be trained in the carer-led massage.

Stakeholder interviewees suggested ways of disseminating the massage training materials to reach the people who matter most: those with NBD and HCPs dealing with these issues. To that end, PwMS would need to be given access to videos and other training resources, and HCPs would need to be trained in the intervention and how to teach it. Stakeholders suggested that a number of key organisations should be included in approaches to dissemination of training and, when appropriate, training materials could be hosted on their websites:

• National Institute for Health and Care Excellence (NICE)

• NHS England

• Royal College of Nursing

• Association for Continence Advice

• MS Society

• MS Trust

• Association of British Neurologists

• UK MS Nurse Association.

Process evaluation discussion

The experiences of PwMS provide powerful illustrations of how constipation can have a wide-ranging, negative effect on their everyday lives. Quality of life is severely impaired, to the extent that some people are afraid to leave their homes and may end up socially isolated, anxious and in pain. Interviews revealed the vicious cycle of symptoms, such as reducing food intake and disturbed sleep as a result of laxative use, and the fatigue commonly associated with MS17 was exacerbated by constipation. Despite the symptom burden, there are few evidence-based treatments available and the cost to the NHS of dealing with constipation is substantial. 61

The findings from the process evaluation demonstrate the potential for abdominal massage to be adopted as a bowel management technique more widely within the NHS. Seventy-five per cent of interviewees (n = 15) experienced improvements in their symptoms, and we were able to offer possible explanations for the lack of improvement in others. In some instances, it would be more appropriate to report that there were only minor improvements rather than none, but these minor improvements were not detectable via primary and secondary outcome measures in the main trial. It seemed that only the more dramatic improvements were able to be captured. The training focused on supporting patients to administer the massage themselves and, although the AMBER trial protocol did include the option for carer-/partner-administered massage, this option may have been missed by those unaware at the outset that they did not have the physical dexterity to perform the massage effectively.

Most of the sites involved in the trial were not currently using abdominal massage as a form of treatment and the consensus, from both HCPs and stakeholders, was that bowel problems in PwMS had to be better managed. The interviews revealed that most participants intended to continue with the massage, demonstrating the acceptability of this noninvasive treatment.

The process evaluation presents results of an approach that draws on longitudinal interviews. Following both trial participants and trial delivery over time allowed us to track processes of change and offer explanations for trial outcomes. The finer nuance achieved by bringing together interviewee experiences with bowel diary data offered insights that suggest that the outcomes may actually be more positive than the statistical analysis suggests. Furthermore, arguably, the AMBER trial achieved greater value by incorporating insights on trial processes. While being mindful of the need to protect trial equipoise, the process evaluation team worked closely with the trial team to establish a feedback loop to report anything that could be easily addressed without affecting the intervention itself. For instance, the time burden associated with compiling information packs was reported back to the trial team and they subsequently changed the format of recruitment packs to address this. This ensured that HCPs within the sites felt listened to and it encouraged them to reflect on the trial and share their feedback with us.

Capacity issues at sites mainly affected recruitment levels in the trial. Understaffing, part-time contracts and hectic workloads meant that staff members were limited in the amount of time that they could spend on the trial. As some sites were already offering massage, this also meant that there were few eligible participants to recruit. Interestingly, it was reported across all sites that participants randomised to the control group of the trial were disappointed, but the retention rate was higher in this group. This may be because the control group had a greater incentive to remain in the trial until the end, when they would be offered the opportunity to learn the massage technique. Control group retention may also have been positively affected by the telephone support offered by site staff. This may also have contributed to fewer differences between intervention and control group outcomes, because site staff gave advice on medications as well as lifestyle.

What may be extrapolated from our process evaluation is that there is the potential for massage to improve the symptoms of NBD; this in turn may then lead to reduced hospitalisations, reduced prescriptions, amount of time HCP spend with patients and improved quality of life for PwMS. The main macrolevel changes from the massage are said, by interviewees, to be freeing up staff capacity in the long term and greater quality of life for PwMS. The argument would need to be made that the short-term work and costs associated with implementing massage training would save money in the long term.

Health-care professional and stakeholder interviewees expressed interest in implementing abdominal massage in the longer term. A number of sites were willing to adopt abdominal massage as a form of treatment and many of these interviewees felt that there was potential to roll this out to wider population groups, in a range of health and community settings. Finally, the words of our trial participants are worth repeating:

It made a terrific difference, in fact I have to make myself look back to see how bad things were because there’s a terrific improvement, yes. It’s made an awful lot of difference to me ‘cause things were really bad to start with, but they’re a lot better now.

PwMS1_2

There are some strengths and limitations to the process evaluation. Strengths include the fact that although we were unable to purposively sample, nevertheless the convenience sample yielded a participant mix that reflected our initial hypotheses regarding time since diagnosis, severity of symptoms and sex. This enabled us to capture robust data from which to explore potential variations in the experiences of trial participation (PwMS), trial delivery (HCPs) and to reflect on issues of potential future implementation and sustainability. The HCP interviews all included at least one staff member involved in delivering the trial at each site. This allowed the researcher to identify any challenges around recruitment or other trial processes that could be fed back to the trial management team. Another strength was the longitudinal nature of the research, thus facilitating scope for follow-up on any problems raised during the original interviews and exploration of the longer-term impact of abdominal massage. This is a methodological innovation rarely accomplished within process evaluations and is a major strength of the AMBER trial. Similarly, interviewing HCPs in two stages provided an opportunity to talk to additional staff members who had become involved in the trial later on, allowing for the exploration of contextual factors, such as change in capacity over time, that might have negatively affected trial delivery and implementation.

There are, however, some limitations to the process evaluation study. Owing to limited resources, only those in the intervention group were recruited for interview; therefore, we could not explore any contexts experienced by control group participants that might also have had an effect on outcomes. Another potential limitation was that those who agreed to be interviewed were likely to have had a higher level of engagement with the trial; thus, they may have been both more likely to fully participate in the intervention and to remain in the trial until its completion. However, our analysis of bowel diaries linked to interview participants revealed that they had variable levels of adherence to the massage. Although all interviewees remained in the trial, interviews with those that did withdraw would have been informative. Finally, participants’ expectations of the trial were not associated with positive or negative outcomes, suggesting that our conclusions regarding their trial experiences and outcomes can be used to interpret wider trial outcomes. As only 12 sites (hospitals in Scotland and England) were involved in the trial, and our stakeholder interview numbers were small, the results cannot be seen to be representative of health-care services across the whole of the UK.

Adherence

According to the self-completed diary, which recorded the frequency of undertaking the massage, adherence to the massage intervention was good; 75% of participants administered the massage five times per week, although, interestingly, the vast majority were undertaking self-massage. At week 24, 66% of participants were continuing with the massage at least three times per week. In the qualitative interviews, participants reported that they practised the massage when it fitted into their routine and altered it according to effect, that is they did not necessarily do it every day. In fact, one person felt it to be too effective if undertaken every day.

The adherence to changing lifestyle, such as diet and exercise, was slightly greater in the control group, with 30% (20% in the intervention group) saying that they had made at least one lifestyle change. Such changes may have facilitated the changes reported within the control group. The overall uptake of the suggested modifications, supported and discussed at the weekly telephone calls, was perhaps lower than expected and is in contrast to what was reported in the qualitative interviews in which the participants said that they found the information to be helpful. To that end, discussing it with the nurse should have aided implementation in both groups. However, those in the control group were not interviewed (a limitation of the study), so there is no feedback as to how they felt about the delivery of the advice. It is a recognised feature that for some PwMS, the processing of such information is difficult and requires frequent, spaced reinforcement.

Who benefits and why?

Abdominal massage is thought to work by stimulating the bowel and decreasing the overall transit time; thus facilitating defaecation by the stronger propulsion of stools that are less hard and difficult to evacuate. Within our anorectal substudy, it was identified that 60% of this subgroup demonstrated slow transit; if we could extend this frequency of slow transit to the whole study group then it may, to some extent, explain why the response was varied and less than expected. Patients may also have anorectal dyssynergia, which can make it difficult to pass stool; if this was the primary reason for their constipation, then abdominal massage would have little effect. However, slow transit and dyssynergia often coexist and, unfortunately, owing to poor uptake of the follow-up anorectal outcomes, we can only speculate and identify this as an area requiring further investigation. Given the small improvement in the primary outcome but not in terms of QALYs, a low-cost version of the intervention might be considered worthwhile by some patients. For example, it could be a part of a supported self-management pathway for NBD in PwMS.

Our data indicate consistently that the male participants reported better outcomes from the intervention. Although only a small group (n = 14 in the intervention group and n = 21 in the control group), the reasons behind these findings are unclear (see Tables 18 and 19). It may be that the male participants were stronger and less fatigued and undertook the massage more effectively. To date, we do not know the amount of force that is needed to be effective in stimulating the bowel. Within our qualitative study, a theme emerged around the adaptations made as a result of fatigue and difficulties actually doing the massage; yet there was also a theme that this was something PwMS wanted to do themselves, so as not to increase care burden, and a way of improving symptoms without taking medications. The amount of pressure and an assistive device to help with self-massage are potentially other avenues that should be explored. There was also some evidence that those with a slightly higher BMI, those who were slightly older, those who were less cognitively impaired and those with relapsing–remitting MS improved with the abdominal massage more than those with a lower BMI, who were younger, more cognitively impaired and did not have relapsing–remitting MS. Potentially, the older participants may be retired and have more time; however, why the slightly heavier people should improve more is difficult to explain.

Medication

Constipation was linked to laxative usage, which could also result in negative side effects. Interviewees reported that taking laxatives caused pain, sleeplessness, cramps and diarrhoea. The unpredictability of passing a stool when taking laxatives meant that a number of patients were afraid to leave the house once they had taken laxatives. From the analysis of laxative use, it would seem that those in the intervention group were more likely to reduce their laxative use. Participants’ overall medication change was monitored and the number of medications seemed to change more in the control group; however, this was difficult to analyse as several participants had multiple changes and, in one instance, suppositories were individually mentioned. It was, however, interesting to see the history of the prescribing of laxatives, where it seemed to be the norm to increase the dose as well as prescribing additional laxatives within a short space of time.

This is an intervention for which we found no evidence of harm and which does not require extensive resources or training. There were a small number of AEs, none of which could be directly attributable to the massage. Moreover, this is the first time that the reduced training, to both clinicians and participants, was rolled out. In our earlier studies, those teaching the massage to the participants were experienced continence clinicians and the participants received weekly follow-up visits for support. In this trial, some of the clinicians had no experience of treating either bladder or NBD and only one had pre-trial experience with the massage. Feedback from clinicians was very supportive of the intervention and our recruitment is testimony to this. Some reported that further training may have been helpful and this is understandable if a ‘hands-on’ concept was new and also the lifestyle information was not within their usual scope (clinicians comprised MS nurses, continence nurses, a research nurse and one research assistant). However, as shown in our secondary and sensitivity analyses (see Tables 18 and 19), results were not significantly dependent on sites and the experience of the researchers.

If this intervention was to roll out within the NHS, then we suspect that it would depend on local services to facilitate staff training; yet, where these staff sit (e.g. the continence service or the MS nurse service) is undecided at the moment. Remarkably, there was no feedback from participants that they would have preferred more training or support with the massage. The interviews did highlight that, during the initial training, some people preferred the massage to be administered over their clothes or on body parts other than their stomach. This may have affected how the staff member was able to deliver training, because the massage should be administered on the abdomen in order to allow the patient to gauge pressure. The clinicians interviewed all remained enthusiastic about the intervention, which influenced the mainly positive feedback participants were giving to them. Those used to treating PwMS recognised that interventions to treat the symptoms of NBD are scarce and that this could be a part of their ‘toolkit’, as an adjunct or perhaps instead of, for instance, laxatives, rectal irrigation, biofeedback, none of which is evidence based. Stakeholders also recognised that there was a definite need for additional treatment modalities and that this is a relatively cheap intervention if, after appropriate assessment and training, it is undertaken by the patient themselves or a carer. Additional resources may, however, be required should NHS employees be required to administer the massage routinely.

Limitations

There are several limitations in this study. The differential numbers recruited to our two groups (attributable to minimisation by centre) coupled with the additional numbers in the intervention group who failed to complete the study meant that we ended up with a smaller number in the intervention group than we had hoped. The extent of missing data and the reasons behind it have been explored but do not seem to be related to any predictable factors. One site, UCH, London, which undertook the anorectal physiology tests, had a slightly lower retention rate (76.9%); this may have been because of the invasive nature of these tests and the unwillingness of participants to return for follow-up. Royal Preston and the Walton Centre both had a retention rate of 81%, but no specific pattern for loss to follow-up could be identified as reasons were varied and appeared unconnected to the intervention (e.g. family illness, moving location).

It may also have been better to use more stringent inclusion/exclusion criteria, such as Rome III,63 as some participants were not severely affected (according to the primary outcome measure) by their constipation and, therefore, had limited capacity to improve. These criteria had been used in a previous study by the authors, but were felt to be too stringent, focusing, as they do, on a clinical expert definition rather than a patient-based or a combined clinician–patient definition of constipation. Indeed, the suitability of the Rome III criteria for assessing symptoms of constipation has been challenged, as studies show that many patients who report constipation symptoms do not fulfil the Rome III criteria. 64–66 Patients’ perception of ‘bothersomeness’ seemed to fit better. A large number of participants undertook the massage themselves, but because of their weakness and fatigue the effectiveness may have been reduced. Several participants in our qualitative study stated some difficulty self-massaging because of fatigue, but tried to work out a way around it by, for example, taking rests. However, for some participants, the massage was probably undertaken at a suboptimal level. Within our process evaluation study, owing to financial constraints, the interviews were only conducted with those who were undertaking the abdominal massage, which poses a limitation on our knowledge of the uptake of the advice and perceptions of taking part in the trial as part of the control group. The limitations in the economic evaluation have already been discussed in Chapter 4.

Future research

It would seem from the results of the RCT, the qualitative study and the health economic component that, similar to other studies, abdominal massage is effective on some patients. Most likely, these would be patients who have primarily slow transit (potentially 60% in this study). Therefore, future research should focus on identifying those with slow transit, which, as our anorectal substudy showed, is not easy to do using invasive tests. There have been attempts to validate questionnaires (e.g. Kess Questionnaire66) that may indicate which type of constipation a person has, that is slow transit and/or dyssynergia, and these should first be validated in a MS population and then used for possible screening of those with predominant slow transit constipation. In addition, the optimum frequency and, importantly, intensity of massage should be explored with use of pressure-sensitive devices and massage devices.

The following is a list of recommendations for future research:

• further mechanistic evaluation of NBD and ways of identifying those with predominantly slow transit

• further validation of the NBIS questionnaire

• development of a treatment algorithm that would aid clinicians in the treatment of NBD

• development and evaluation of a device to aid abdominal self-massage

• development and clinical trials of other interventions that may help with the symptoms of constipation/FI, for example the superfruit baobab, which has recently been developed into a drink, Baotic (Hippo & Hedgehog Ltd, Glasgow, UK).

The AMBER trial group

Principal Investigators: Dr Stewart Webb, Dr Martin Duddy, Dr Anton Emmanuel, Dr Roger Mills, Dr Carolyn Young, Mr Matt Craner, Mrs Nicki Stubbs, Professor Basil Sharrack, Dr David Rog, Mrs Emma Matthews and Dr Belinda Weller.

Tayside CTU for their assistance with randomisation, data management and statistical support.

All members of the DMEC and TSC for their advice and support throughout the trial.

Staff at all 12 UK sites for their hard work throughout the trial: Queen Elizabeth University teaching Hospital, Glasgow; Royal Victoria Hospital, Newcastle upon Tyne; UCH, London; Royal Preston Hospital, Preston; The Walton Centre, Liverpool; John Radcliffe Hospital, Oxford; St Mary’s Hospital, Leeds; Lincoln County Hospital and Pilgrim Hospital, Lincoln; Salford Royal Hospital, Salford; Royal Hallamshire Hospital, Sheffield; Northampton General Hospital, Northampton; and Anne Rowling Generative Neurology Clinic, Edinburgh.

Our PPI group who gave their time, views and opinions, and who remained enthused about the study throughout the 3 years of their involvement.

All the AMBER trial participants for the time and commitment they gave to the study.

Contributions of authors

Professor Doreen McClurg (Chief Investigator and lead grant holder and member of the PMG/TSC) conceived the study and led on the protocol development, analysis and interpretation of the data, and drafting and submitting the final report.

Dr Fiona Harris (Associate Professor, grant holder and member of the PMG/TSC) led and supervised the process evaluation component of the trial and contributed to the analysis and drafting of the final report.

Dr Kirsteen Goodman (Trial Manager and member of the PMG/TSC) contributed to the running of the trial, data management, interpretation of results and drafting the final report.

Dr Selina Doran (Qualitative Researcher and member of the PMG/TSC) conducted the process evaluation data collection and analysis and contributed to drafting the final report.

Professor Suzanne Hagen [Interventions Programme Director (NMAHP RU), grant holder and member of the PMG/TSC] contributed to the study design, provided clinical expertise throughout the study and reviewed the final report.

Professor Shaun Treweek (Professor of Health Services Research, grant holder and member of the PMG/TSC) contributed to the study design, provided clinical trial expertise throughout the study and reviewed the final report.

Professor Christine Norton (Professor of Nursing, grant holder and member of the PMG/TSC) contributed to the study design, provided clinical expertise throughout the study and reviewed the final report.

Dr Maureen Coggrave (Research Fellow, grant holder and member of the PMG/TSC) contributed to the study design, provided clinical expertise throughout the study and reviewed the final report.

Professor John Norrie (Chair of Medical Statistics and Trial Methodology, grant holder and member of the PMG/TSC) contributed to the study design, provided clinical trial expertise throughout the study and reviewed the final report.

Miss Petra Rauchhaus (Trial Statistician at TCTU and member of the PMG and TSC) contributed to the trial analysis and reporting of results.

Professor Peter Donnan (Co-Director of TCTU, Senior Trial Statistician, grant holder and member of the PMG/TSC) led on the statistical aspect of the trial design and analysis of data, contributed to the drafting and review of the statistical sections of the final report.

Dr Anton Emmanuel (Senior Lecturer and Consultant Gastroenterologist, grant holder, member of the PMG/TSC and a PI) contributed to the study design and provided clinical expertise throughout the study and reviewed the final report.

Dr Sarkis Manoukian (Health Economist and member of the PMG/TSC) led on the health economic aspects of the trial design, interpretation of the data and drafting the health economic section of the final report.

Dr Helen Mason (Reader in Health Economics, grant holder and member of the PMG/TSC) led on the health economic aspects of the trial design, interpretation of the data and drafting of the health economic section of the final report.

Publication

McClurg D, Goodman K, Hagen S, Harris F, Treweek S, Emmanuel A, et al. Abdominal massage for neurogenic bowel dysfunction in people with multiple sclerosis (AMBER – Abdominal Massage for Bowel Dysfunction Effectiveness Research): study protocol for a randomised controlled trial. Trials 2017;18:150.

Data-sharing statement

All data requests should be submitted to the corresponding author for consideration. Access to anonymised data may be granted following review.

Patient data

This work uses data provided by patients and collected by the NHS as part of their care and support. Using patient data is vital to improve health and care for everyone. There is huge potential to make better use of information from people’s patient records, to understand more about disease, develop new treatments, monitor safety, and plan NHS services. Patient data should be kept safe and secure, to protect everyone’s privacy, and it’s important that there are safeguards to make sure that it is stored and used responsibly. Everyone should be able to find out about how patient data are used. #datasaveslives You can find out more about the background to this citation here: https://understandingpatientdata.org.uk/data-citation.

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 HTA 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 HTA programme or the Department of Health and Social Care.

Differences in continuous characteristics of missing Neurogenic Bowel Dysfunction Score at 24 weeks compared with complete data

Summary of serious adverse events

Frequency of health-care contacts, by trial group, recorded at week 6

Frequency of health-care contacts, by trial group, recorded at week 24

Total frequency of health-care contacts, by trial group, excluding baseline

Resource-use NHS costs per participant, by trial group, at baseline

Resource-use NHS costs per participant, by trial group, at 6 weeks

Resource-use NHS costs per participant, by trial group, at 24 weeks

Stakeholders selected for interview

Intervention group

Health-care professionals

Stakeholders

• The organisation’s role in neurological and/or incontinence services.

• Current policy developments in this area (local, regional and national).

• Current treatment options for bowel problems, particularly neurogenic ones.

• Whether or not there is a need for an additional treatment option.

• The long-term implementation of abdominal massage and any challenges involved.