Mood, Activity Participation, and Leisure Engagement Satisfaction (MAPLES): results from a randomised controlled pilot feasibility trial for low mood in acquired brain injury

The primary objective of the Mood, Activity Participation, and Leisure Engagement Satisfaction (MAPLES) trial was to determine the feasibility and acceptability of two activity-based group interventions in adults with ABI with low mood and/or activity levels, as per our trial protocol [30]. Feasibility and acceptability were assessed via participant retention from baseline to 1-month post-intervention, acceptability of group sessions and assessments, and qualitative interview feedback. Although originally planned to occur completely in-person, the COVID-19 pandemic and resulting social distancing regulations meant that the study pivoted to online delivery in March 2020. This offered the opportunity to compare the two forms of delivery. Therefore, we report combined results and, where appropriate, in-person and online results separately.

The secondary objective was to explore whether either Traditional (AP) or Experiential (AE) Behavioural Activation leads to changes in activity levels and related outcomes, including depression, anxiety, post-traumatic stress, motivation, participation, and sense of control. To control for repeated exposure to assessments, and to ensure all participants were able to receive a potentially helpful intervention, AP and AE participants were compared to a waitlist control (WL) condition in ABI as per Kahan et al. [31].

MAPLES is a 1:1:1 parallel arm randomised controlled trial with nested qualitative research. A CONSORT checklist is in Additional File 1.

The UK National Health Service Health Research Authority (REC reference: 18/EE/0305) provided ethical approval. The study was registered at clinicaltrials.gov on March 12, 2019 (NCT03874650). All participants provided informed consent prior to participation. Approval to conduct groups online was obtained June 5, 2020.

Participants were recruited from two NHS sites in Cambridgeshire, UK. In-person sessions were held in NHS sites or at the MRC Cognition and Brain Sciences Unit. Following the onset of COVID-19, non-COVID research was halted across all NHS Trusts. Recruitment expanded to ABI research panels, ABI charities, and self-referrals (ABIs verified by research team via medical record access) via social media. These sessions were delivered online using videoconferencing.

Inclusion criteria:

Exclusion criteria:

Individuals with mild traumatic brain injury were not excluded from accessing the trial provided a confirmation of diagnosis from medical records. In the protocol [30], we additionally excluded participants who were currently undergoing or due to undergo a psychological intervention during the trial. This criterion was removed in agreement with the Steering Committee as, in practice, excluding potentially eligible participants who met with a therapist infrequently (e.g., once every 3 months) was a recruitment barrier. Differences in proportions of those receiving any type of therapeutic input across study arms was assessed.

Both groups met for approximately 1.5 h once weekly over 8 weeks. Group sizes ranged from 3 to 6 individuals. WL participants received no intervention for an 8-week period between first and second assessments. The interventions are described briefly below. Detailed descriptions are in the study protocol [30].

Both groups were facilitated by AK1. AK1 received intervention training (approximately 6 h) and regular supervisions from senior research team members, which included a registered clinical psychologist (TM).

The AP group was designed based on typical BA interventions (see Kanter et al. [33]) and interviews with ABI participants and carers [34]. AP sessions centred on increasing engagement in meaningful and positive activities. Participants were instructed to “task split” planned activities into steps and monitor their mood and activities to help identify connections between the two [8, 35]. Participants identified counter-productive avoidance patterns, including distraction and goal neglect (not completing a stated intention [36]), and practiced strategies to overcome these [21, 37]. Session content is described in brief in Table 1.

AE participants received no specific encouragement to increase activity engagement between sessions or to overcome barriers to activity participation in everyday life. Rather, they were told that they would complete potentially rewarding activities during sessions. At the start of the 8 weeks, participants were told that one approach to increasing activities was to “learn by doing” and as part of the group they will take part in potentially reinforcing/enjoyable activities. Participants were offered suggestions, such as card games and “pub quizzes,” and were encouraged to suggest activities (including repeating an activity from a previous session). Session content was based on typical ABI charity activities. Over the course of the 8 sessions, participants were encouraged to jointly discuss which activities they would like to complete.

One-third of participants were first assigned to WL. At the end of the 8-week waiting period, participants completed a second baseline assessment and were immediately re-randomised into either AP or AE. To produce unbiased estimates, the WL design followed the recommendations of Kahan et al. [31], where re-randomisations were (1) conducted only after the WL period was completed and (2) conducted independently from the initial randomisation sequence. Further, potential effects of either BA group were assumed to have comparable effects across randomisations [31].

Group sessions were audio recorded to assess intervention fidelity. Two research assistants not conducting the intervention retrospectively listened to 25% (42 h) of sessions. AP group fidelity was assessed in terms of whether intervention components were delivered. Given the nature of the AE group, general principles (e.g., not discussing planning activities outside of sessions) rather than specific content were used to evaluate fidelity (see Additional File 2: Document S1 for Fidelity checklists). Research assistants followed the below steps [38]:

Following steps 2 and 3, raters compared their scores and resolved discrepancies, if any. Sufficient agreement was considered reached once raters had less than 10% discrepant items, after which ratings were completed independently. All rating checklist items were summed and given percent scores per checklist, per group. Percent scores were then averaged for a total estimate.

Feasibility and acceptability were determined based on targets set out in the accompanying protocol paper [30]:

Because the key aim of BA is to increase engagement in activities, the Behavioural Activation for Depression Scale (BADS [39, 40]) was selected as the primary efficacy outcome measure. The BADS is a 25-item measure of activation and avoidance behaviours underlying depression. Higher scores indicate greater activity engagement (“behavioural activation”).

Participants were recruited for 18 months and enrolled in 7 successive cohorts or “waves”.

The primary objective was to determine feasibility and acceptability. Approximately 20 participants per arm (total 60) was considered sufficient to balance between determining feasibility and exploring treatment effects [41].

Participants recruited through any source were first given invitation letters, providing a brief study summary. Interested individuals were screened to determine eligibility. If eligible, an appointment was made to take informed consent and conduct the baseline assessment.

Pre-determined block randomisation with blocks of varying length was generated by the trial statistician and was unknown to the rest of the team. Participants first assigned to WL were re-randomised using pre-determined block randomisation.

Quantitative assessments at Times 2 and 3 were conducted by condition-blinded research assistants. It was not possible for researchers conducting qualitative interviews (that discussed specific group experiences) to be blind to condition.

Depending on COVID-19 restrictions, participants gave informed consent in-person or via videoconferencing. Participants optionally provided consent for researcher access to medical records for ABI details. Demographic information, such as age, gender, ethnicity, and occupational status, were recorded. Participants then completed the baseline assessment (Time 1). AP and AE participants received a post-intervention (Time 2) and 1-month follow up (Time 3) assessment. Participants first randomised to the WL group completed a second baseline assessment (Time 2) prior to being re-randomised into either the AP or AE group.

Detailed descriptions of secondary outcome measures are in the trial protocol [30]. Secondary outcome measures were selected by whether each was an expected outcome of BA (activities, mood, anhedonia; community integration) or a theoretically relevant process to improvements (approach and avoidance behaviours, coping with uncertainty, motivation, locus of control).

Depression and anxiety were measured using the 14-item Hospital Anxiety and Depression Scale (HADS [32]), with possible scores on subscales (HADS-Depression and HADS-Anxiety) ranging from 0 to 21. Example items include “I still enjoy the things that I used to” (HADS-Depression; reverse coded) and “I feel tense or ‘wound up’” (HADS-Anxiety). Higher scores indicate greater depression/anxiety.

To assess approach- and avoidance-motivated behaviours toward activities, the 20-item Behavioural Inhibition Scale/Behavioural Activation Scale (BIS/BAS [42]) was used. The BIS scale ranges from 7 to 28 (example item: “I worry about making mistakes), while the BAS portion comprises 3 subscales: Drive (“I go out of my way to get things I want”; range 4–16), Reward Responsiveness (“When I get something I want, I feel excited and energised”; range 5–20), and Fun Seeking (“I crave excitement and new sensations”; range 4–16). Higher scores indicate greater inhibition (BIS) or activation (BAS).

To assess difficulties with coping with uncertainty in activities, the 12-item Intolerance of Uncertainty Scale – Short Form (IU-SF [43]) was used. The IU-SF comprises two subscales: Prospective (“I always want to know what the future has in store for me”; range 7–35) and Inhibitory (“When it’s time to act, uncertainty paralyses me”; range 5–25). Higher scores indicate greater difficulties with either Prospective or Inhibitory uncertainty.

To assess post-traumatic stress symptoms, the 22-item Impact of Events Scale-Revised (IES-R [44]) was used. The IES-R has three subscales: Intrusion (“Pictures about [my injury] popped into my mind”; range 0–35), Avoidance (“I tried not to think about [my injury]”; range 0–40), and Hyperarousal (“I felt watchful and on guard”; range 0–35). A total score can also be calculated (possible range 0–110). Higher scores indicate greater post-traumatic stress.

To assess internal motivation, the 34-item Brain Injury Rehabilitation Trust Motivation Questionnaire-Self (BMQ-S [45]) was used. Total scores range from 34 to 136, with an example item including “I avoid doing things I don’t have to”. Higher scores indicate greater difficulties with internal motivation (i.e., not motivated).

To assess motivation for rehabilitation-related activities, the 31-item Motivation for Traumatic Brain Injury Rehabilitation Questionnaire (MOT-Q [46]) was used. The MOT-Q has four subscales: Lack of Denial (“I don’t have any problems worth mentioning”; range − 16 to + 16), Interest in Rehabilitation (“Rehabilitation is very useful”; range − 14 to + 14); Lack of Anger (“Therapists would have me do things that are irrelevant” [reverse coded]; range − 20 to + 20) and Reliance on Professional Help (“I rely on doctors to help me with my problems”; range − 12 to + 12). Higher scores in each subscale indicate greater motivation.

To assess community integration, the Modified Outcome Measure – Participation Objective, Participation Subjective (MOM-POPS [47]) was used. This is a shortened version of the POPS scale. Participants rate actual engagement in household, occupational, and social activities in the past week (Participation Objective score) and whether actual engagement differs from their ideal level of engagement in these activities (Participation Subjective score). Participants additionally list types of activities engaged in the past week (e.g., cleaned the house, made social arrangements).

To assess hedonic capacity, the 14-item Snaith-Hamilton Pleasure Scale (SHAPS [48]) was used. Total scores range from 0 to 14, with an example item including “I would be able to enjoy a beautiful landscape or view.” Higher scores indicate greater hedonic capacity.

To assess locus of control, the 12-item Sense of Control Scale (SCS [49, 50]) was used. The SCS comprises two subscales: Personal Mastery (“I can do just about anything I really set my mind to”; range 8–56) and Perceived Constraints (“There are many things that interfere with what I want to do”; range 4–28). Higher scores indicate greater perceived mastery or constraints, respectively.

The Verbal and Spatial Reasoning Test (VESPAR [51]) was conducted to assess cognitive function at Time 1 only. The VESPAR is a neuropsychological test of inductive reasoning using word- and picture-based subtests. Here, we used the Verbal Odd One and Spatial Odd One subtests.

At baseline only, participant expectations and credibility of their allocated group was assessed using the 6-item Credibility/Expectancy Questionnaire (CEQ [52]). The CEQ comprises two factors: Expectancy (“What percent improvement do you think will occur?”) and Credibility (“How confident would you be in recommending this group to a friend?”).

At Time 3, participants completed a custom-designed Post-Study Questionnaire (PSQ) on group experiences and factors affecting participation (see Additional File 2: Document S2).

Twenty participants completed an exit interview at Time 3, comprising in-depth questions about group experiences. AP participants additionally provided feedback on content and materials (see Additional File 2: Document S3 for interview script).

Individuals taking part in-person received travel reimbursement. All participants received a £50 remuneration at Time 3.

Measures with < 20% of missing items had total scores imputed based on averaged responses from answered items (occurred in < 5% of cases). Any measure with > 25% missing items was treated as a missing value for a participant (< 5% of cases).

WL Time 2 assessments served two purposes. These were used for comparison with Time 2 AP and AE data and also used as pre-group attendance baseline scores (i.e., effectively “Time 1”) to examine any changes post-AP or -AE group in former WL participants.

Quantitative analyses were conducted on feasibility, acceptability, and potential efficacy measures across AP, AE, and WL groups in order to determine whether trial outcomes differed as a result of initial condition allocation (e.g., greater attrition in WL participants, greater AP or AE changes in activity levels compared to no intervention).

Percent attrition rates, at what point attrition occurred, number of sessions attended (mean and median estimates in the event of extreme values), and group helpfulness and enjoyableness ratings, were calculated to inform feasibility and acceptability conclusions. Missing data and reasons for drop-out and non-attendance are reported.

Quantitative data were analysed using R statistical software version 4.1.2 [53] using an intention-to-treat analysis. Demographic variables per group are reported. Unadjusted mean differences from baseline to post-intervention between AP, AE, and WL arms with 95% confidence intervals were estimated. The Minimal Clinically Important Difference (MCID; see Results for details on calculation) of the BADS and secondary efficacy outcomes were estimated. A linear mixed-effects model using the BADS across time points was conducted. Exploratory analyses were conducted to estimate the effectiveness of the AP and AE groups and determine effect size estimates for a definitive trial power analysis. All data and associated code are available on the Open Science Framework database: https://​osf.​io/​e5btr.

Qualitative data were transcribed verbatim by the first author (AK1) and research assistants (EC1, AK2, WW), with personally identifiable information removed. Qualitative data were analysed using an interpretive description thematic summary framework [54], analysed by AK1. Interpretive description aims to build clinically relevant themes and was thus deemed an appropriate method for the trial. Transcripts were analysed in sequence to build an initial codebook of potential themes that were later refined following further analysis. Given the focus on acceptability of the groups, greater description via a larger number of smaller themes was preferred (versus a more interpretive analysis of overarching themes).

As all participants received the PSQ, and 30% of participants received the exit interview, pre-specifying saturation was not possible. Potential themes relevant to acceptability were discussed in peer debriefing sessions among the supervisory team and with patient representatives using select transcripts of participants reporting positive and negative group experiences. Constructed themes were considered in light of the reflexivity entries completed by research assistants conducting the interviews and were informed by quantitative self-reported helpfulness and enjoyableness ratings of participants. Pseudonyms are used to present the data.

Management and reporting of adverse events were conducted as per MRC protocol. Any cases of adverse events or harms are reported, alongside consideration of any potential harms due to the interventions.

Due to COVID-19 requiring completely remote research, feasibility data were summarised for in-person and remote sessions separately.

Recruitment targets were met only when including re-randomised WL participants; otherwise, minimum recruitment targets were only met for Wave 1 and Wave 4 (Table 3).

Before the first UK COVID-19 lockdown (March 23 2020), the majority of participants recruited were from NHS ABI services (19 of 25). During COVID-19, participants were mostly recruited from ABI charities (22 of 35; see Additional File 2: Table S2 for eligibility per recruitment source). Self-referral via social media was the most efficient referral route (14 of 21 screened randomised; 66.7% eligible).

When including re-randomised participants, attrition was less than 20% across the three arms (Table 4). Not including those re-randomised, withdrawal rates were 13.6%, 9.1%, and 18.8% in AP, AE, and WL, respectively.

The most common reason for withdrawal was difficulties travelling to the study location (n = 3; 1 per trial arm), followed by expressive aphasia affecting group participation (n = 1 AP and n = 1 AE) (see Fig. 1 for all reasons).

Including participants who withdrew, average attendance did not differ between the AP and AE group (t =  − 0.38, p = 0.70; Table 5). However, median attendance rose from 7 to 8 when delivered online. Average attendance did not differ in-person or online for the AP (t =  − 1.25, p = 0.22) or AE group (t =  − 0.55, p = 0.59). Session attendance per wave and reasons for non-attendance are in Additional File 2: Figures S1 and S2.

PSQ and exit interview qualitative data were used to explore perspectives of acceptability, specifically aspects that positively or negatively contributed to helpfulness or enjoyableness, of the groups and overall participation in the study. Table 7 synthesises perceived strengths of the groups or areas for improvement, with example quotes in Additional File 2: Table S4. Recommendations presented below should be considered within any local context of recreating the groups described here. For space, in-depth qualitative data analysis of specific group experiences will be reported elsewhere.

The secondary objective was to provide estimates on the primary efficacy outcome measure and sample size determination for a subsequent trial. We summarise missing data, AP and AE fidelity assessment results, and efficacy estimations on the primary efficacy outcome measure between groups.

The MCID for all outcome measures was calculated using the standard error of measurement (SEM):

Sigma (\(\sigma\)) was Time 1 standard deviation and the reliability (r) was Time 1 internal consistency. Time 1 to Time 2 data were used to calculate percent estimates across groups, including those re-randomised. For the BADS, the MCID was 8.28. Missing data at Time 2 was imputed using predictive mean matching (PMM) across 5 imputed datasets via the mice R package [57].

BADS MCID change from Time 1 to Time 2 between groups using complete cases (including those re-randomised) are in Fig. 5, where 58.33% of AP participants showed BADS improvements at or above this minimally clinically important level, versus 52.17% of AE participants and 30.77% of WL participants. Across 5 imputed datasets, AP participants had a MCID improvement range of 51.72–65.52% versus AE (range 42.86–57.14%) and WL (range 25–37.5%).

As shown in Fig. 5, there were also MCID on this primary efficacy outcome measure in the opposite direction in all groups (AP 25%; imputed range 20.69–34.48%; AE 17.39%; imputed range 17.86–32.14%; WL 38.46% imputed range 31.25–50.0%).

As part of the trial, a formal steering committee consisting of clinicians, researchers, and an ABI survivor was formed to oversee recruitment and study progress. An overview of challenges in implementing the trial from the steering committee’s perspective is presented in Additional File 2: Document S5. In brief, challenges included efficient recruitment through NHS services relative to ABI charities, online intervention delivery resulting in less fatigue due to travel but affecting group social interactions, ABI participants experiencing difficulties with recalling specific group experiences during the qualitative interview at Time 3, and COVID-19 affecting the range of activities participants could partake in throughout the trial.

In contrast, with the recruited sample size, the AP group was statistically superior to AE and WL in terms of reductions in depression symptoms (HADS-D), anxiety (HADS-A) and intolerance of uncertainty (IU-SF Inhibitory Anxiety), and improvements in motivation (BMQ-S), with over 50% of AP participants demonstrating MCID improvements in anxiety and depression. All of these gains were well maintained one month following therapy cessation, indicating that these may be stronger effects observable in small sample sizes. Given that the current study was not powered to examine these secondary outcome measures, replication of these secondary effects in a newly recruited sample is required. Longer follow-up periods may also be beneficial to assess longer-term maintenance of gains.

There are many potential reasons why, within a BA framework, the desired intervention outcome (improvements in mood) was reliably observed whilst the proposed mechanism (increased activity engagement) was not statistically distinguishable from WL. One possibility is that the relevant measures have different sensitivities; greater activity level increases were enough to reduce depression, anxiety, and related outcomes but were themselves insufficient to cross a statistical threshold with the recruited sample. It is also possible that activity levels increased (at the very least attending the groups and activities within them probably represented an increase for many participants) but that participants were less sensitive to these changes in self-reports relative to mood. Another possibility is that group attendance itself improved mood independently of any activity level change. In an early characterisation of BA, exactly this priming of the mood-activity cycle was posited—“energy level” increases were a prerequisite for activity level increases [61]. If this is the case, changes in activity levels may lag the mood changes but may remain important for the maintenance of mood gains. The results are certainly useful in selecting the most important efficacy outcome measures for subsequent trials and the time-course for assessing change. In terms of enhancing likely effect of groups like AP, greater incorporation of core values assessment throughout may result in greater long-term sustained increases in activities [34, 62].

AE-style groups that have no explicit therapeutic agenda are far less investigated than conventional therapeutic groups in terms of potential mood improvements. These groups can provide a safe and predictable milieu where individuals can form a continuous support network [26, 29] and meet others experiencing similar difficulties to help reduce stigma of ABI [63] that might contribute to activity level increases. Though there was no increase in BADS scores at the recruited sample size, depression symptom reductions were observed and maintained at 1-month following group end, suggesting some lasting impact. Again this is consistent with the notion of an “energy level” boost potentiating subsequent change. Whilst the anxiety and motivation results here certainly suggest that the AP group produced greater benefits, the possibility that AE-like groups could be a useful “BA” intervention for those with marked cognitive problems merits further exploration in a powered sample.

There may be a number of reasons for the apparent superiority of the AP group in mediating greater mood improvement. Firstly, the AP group explicitly encourages participants to plan and engage in between-session positive activities. Second, it incorporates goal management techniques to mitigate barriers to activity engagement. Thirdly, the achievement of these between-session activities may increase a sense of mastery/control that in turn contributed to mood gains [64, 65]. Finally, it is also possible that the AP group serves to modify dysfunctional beliefs and attitudes that are linked with low mood. The rationale for BA over cognitive approaches was never that unhelpful beliefs did not affect mood, but rather these beliefs could be equally or better modified via behavioural experimentation than explicit cognitive restructuring [66‐68]. Changes in motivation, anxiety, and coping with uncertainty in AP participants may reflect changes in unhelpful beliefs about activities. There are likely several factors that explain greater improvements in AP versus AE participants that should be explored in a sufficiently powered sample.

As with all psychological intervention research, interventions can only be single-blinded and therefore completely unbiased effects are not possible. As both interventions were delivered by one person, this minimised the issue of whether “therapy differences” are attributable to “therapist differences” (e.g., confidence, experience). However, this raises the question of whether facilitator beliefs about likely efficacy of each group played a role. Both groups were designed to maximise effectiveness, discussed with a clinical supervisor, and delivered in the knowledge that fidelity would be assessed—which was, as discussed, rated as very high. An important issue for subsequent trials would be maximising facilitator and participant “buy-in” to both approaches to not skew favour toward either approach. There is always the risk that participants who consent to take part in research are not fully representative of the wider population who may be referred to groups in clinical services. In addition, those who self-referred by responding to online invitations may differ in a number of ways from others living with ABI.

Generalisability has benefitted from using a mixed-methods design, in accordance with MRC recommendations [69]. The combination of methods provides richer acceptability and feasibility data and highlights areas to augment in future trials.

A study strength is that circumstances necessitated a variety of recruitment routes, from clinician referrals in NHS services, through charities and from social media self-referrals that can be useful to use in future trials. The blocked randomisation ensured that potential participant differences due to recruitment route would not have a disproportionate impact on any group. Whilst underpowered to examine quantitative outcome differences, the qualitative data at least suggest that both interventions were well-received.

Participants were mainly in the chronic stages of ABI. Earlier stages are associated with greater frequency of impairments and impact on function, which can limit intervention engagement [70]. Some may be less “ready” to accept emotionally focused interventions in early ABI [14]. However, a previous BA intervention in early (within 4 months) stroke reported benefits [71]. ABIs are increasingly being recognised as a chronic condition that require long-term emotional support [72, 73]. It is a study strength to demonstrate that emotional improvement can occur in chronic ABI and greater recruitment from this population may be warranted in community-based NHS settings.

It is likely that improvements in group outcomes in part rely on the degree of cohesion among BA group members. Our trial conducted randomisation at the individual level and therefore pre-selection of similar participants to either group (e.g., in terms of demographics and ABI severity/type of impairments) was not possible. However, our qualitative data indicated that some participants preferred groups comprised of individuals with similar experiences/needs. Future trials should therefore evaluate whether alternative randomisation methods (e.g., cluster randomisation) may be appropriate and incorporate measures of group cohesion as an outcome mediator. Of course, in clinical settings, there is often a balance between using waiting lists to accumulate group participants with similar needs and imposing unduly long waiting times. For this reason, individual therapy provision, or the use of rolling admissions into formerly “static” BA groups to ensure earlier access to an intervention, may be more practical in some cases. Groups such as the Experiential BA group may lend itself to rolling recruitment better than a Traditional BA group that could perhaps be used as a method of positive benefit until a more static Traditional BA group begins.

In protocols for future trials, it may be worth explicitly incorporating how to manage participant delays between baseline assessment and intervention start that strikes a balance between internal and external validity. In clinical practice, participant delays in starting groups (e.g., due to illness, personal circumstances, or return to work dates) may occur occasionally and sometimes intentionally (i.e., in pre-selecting participants who are likely to have good group cohesion). Given we observed three such delays due to personal circumstances within our study, it is likely that a definitive trial will encounter similar situations. One solution could be to pre-specify fixed time windows between baseline assessments and intervention start.

With a mild to moderately depressed sample, it is unknown whether results extend to those with severe depression and therefore further evaluation in severely depressed ABI samples may be warranted. Some participants stated that discussing highly personal and emotionally challenging content was not well-suited to groups. One-to-one support may be preferred in those with more severe depression [74].

Based on data from participants with aphasia, dedicated groups for those with non-fluent aphasia are likely to have greater acceptability [75, 76]. In contrast, people with fluent aphasia given appropriate support and availability of suitable materials appear to benefit from both approaches in our study, though further piloting prior to a definitive trial is needed.

Generalisability must be considered in light of in-person vs. remote delivery. For the former, transport was a considerable barrier for many participants. Transport and access-related barriers relate to community integration and well-being in ABI [77] and are in part responsible for activity level reductions [78, 79]. In-person study results may only be generalizable to those capable of travelling independently or who have carer support in accessing transport; hence, a definitive trial should collect these details alongside recruitment rates.

For online sessions, trading-off limitations (e.g., creating a cohesive group atmosphere online) against higher attendance was preferred by many. Participants with greater physical disabilities and those who found travel too cognitively demanding/tiring particularly benefited. Some online participants, due to service provision differing across regions, could only access groups via videoconferencing. It is certainly possible that our online recruitment benefitted from COVID-19 pandemic lockdowns; it was “something to do” when many other activities and in-person socialisation were restricted. It will be interesting to compare online recruitment rates at times when such restrictions are absent. It seems likely, however, that online and hybrid interventions will become more common given growing evidence of efficacy [80‐83].

Study feasibility and acceptability are relatively robust in the current sample. Though online recruitment enhanced sample diversity relative to in-person recruitment, this still produced a greater number of White British participants relative to UK population data. Hence, generalisation of results to samples more representative of the UK population should not be assumed. Effect size estimates have wide confidence intervals, making it difficult to interpret a true effect of either intervention. Follow-up data at only 1-month post-intervention limits investigation of longer-term effects. The modest sample size prevented meaningful subgroup comparisons between participants with differing ABI severity levels (e.g., mild vs moderate-to-severe TBI) that may relate to degree of acceptability and benefit from the trial. Finally, not recruiting from NHS sources throughout the entire trial limits implementation conclusions for groups in NHS settings with individuals closer to their ABI date and potentially experiencing greater symptom severity, though a detailed account of implementing individual BA in stroke is available [14].

Based on quantitative and qualitative data, as well as steering committee perspectives, recommendations for changes in trial design, recruitment methods, data collection, intervention design, and study outcomes may be beneficial to consider in a main trial (Table 11). Prior to conducting a definitive trial, we recommend evaluating: