Tailored psychological intervention for anxiety or depression in COPD (TANDEM): a randomised controlled trial

Background The TANDEM multicentre, pragmatic, randomised controlled trial evaluated whether a tailored psychological intervention based on a cognitive behavioural approach for people with COPD and symptoms of anxiety and/or depression improved anxiety or depression compared with usual care (control). Methods People with COPD and moderate to very severe airways obstruction and Hospital Anxiety and Depression Scale subscale scores indicating mild to moderate anxiety (HADS-A) and/or depression (HADS-D) were randomised 1.25:1 (242 intervention and 181 control). Respiratory health professionals delivered the intervention face-to-face over 6–8 weeks. Co-primary outcomes were HADS-A and HADS-D measured 6 months post-randomisation. Secondary outcomes at 6 and 12 months included: HADS-A and HADS-D (12 months), Beck Depression Inventory II, Beck Anxiety Inventory, St George's Respiratory Questionnaire, social engagement, the EuroQol instrument five-level version (EQ-5D-5L), smoking status, completion of pulmonary rehabilitation, and health and social care resource use. Results The intervention did not improve anxiety (HADS-A mean difference −0.60, 95% CI −1.40–0.21) or depression (HADS-D mean difference −0.66, 95% CI −1.39–0.07) at 6 months. The intervention did not improve any secondary outcomes at either time-point, nor did it influence completion of pulmonary rehabilitation or healthcare resource use. Deaths in the intervention arm (13/242; 5%) exceeded those in the control arm (3/181; 2%), but none were associated with the intervention. Health economic analysis found the intervention highly unlikely to be cost-effective. Conclusion This trial has shown, beyond reasonable doubt, that this cognitive behavioural intervention delivered by trained and supervised respiratory health professionals does not improve psychological comorbidity in people with advanced COPD and depression or anxiety.

approach (CBA) intervention, which links into, and optimises the benefits of routine pulmonary rehabilitation, with the aim of reducing mild/moderate anxiety and/or depression in people with moderate, severe or very severe COPD.
Phase I -Pre-pilot study -completed (Refinement of the TANDEM CBA intervention manual as a result of focus groups/individual interviews with patients, carers, and health care professionals)

Phase II (Internal pilot and feasibility study) -completed (Separate SAP: Statistical analysis plan_v1.0_Tandem internal pilot) Phase III (Main Trial) -Aim & objectives
To undertake a randomised controlled trial (and a process evaluation) to: 3) Examine the effect of the CBA intervention on carers (where appropriate).4) Determine the cost effectiveness of the CBA intervention from an NHS and personal social services perspective.5) Conduct a process evaluation to inform the implementation of the CBA intervention if the trial is positive, or assist interpretation of findings if it is negative.
Study design Multi centre, two-arm, parallel group, pragmatic, individually randomised controlled, superiority trial including an internal pilot.The designed randomisation ratio is 1.25:1 in favour of the intervention.

Setting
Participants will be recruited from primary and secondary care, and from PR services.The intervention will be delivered in participant's own homes, or at a convenient local (usually NHS) facility, and over the phone.

Participants Inclusion Criteria -Participants
• Adults with a confirmed diagnosis of COPD, post bronchodilator FEV1/FVC ratio <70%.• Moderate, severe or very severe COPD severity on spirometry, FEV1 <80% predicted.• Participants with probable mild or moderate anxiety as determined by the Hospital Anxiety and Depression Scale Anxiety Subscale (HADS-A) scores ≥8 to ≤15; and/or probable mild or moderate depression as determined by Hospital Anxiety and Depression Scale -Depression Subscale (HADS-D) scores ≥8 to ≤15.• Eligible to attend assessment appointment at their local pulmonary rehabilitation service at the time of randomisation i.e. 12 months have elapsed since last undertook PR or participant has another indication for PR referral (e.g.recent deterioration; recent hospitalisation with an acute exacerbation of COPD).• Participants who have been offered PR previously but declined the offer or did not complete PR will be included.

Exclusion Criteria -Participants
• Participants with both HADS-A score and a HADS-D score <8 (within normal range).• Unable to give valid consent.
• HADS-D or HADS-A score greater than 15 (suggestive of possible severe anxiety/depression). • If a referral to PR has been made, the participant is ineligible if they have agreed to attend PR sessions and are due to commence < 4 weeks after the screening visit, (as confirmed in a PR appointment letter or by the PR team).The rationale for this exclusion is that the participant will not have time to receive a sufficient "dose" of the intervention prior to starting PR.

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Tandem Statistical Analysis Plan template V 3.0 Document version 2.0 • Severe uncontrolled psychological or psychiatric disorder e.g.schizophrenia, bipolar disorder, struggling to cope as a result of their personality disorder, uncontrolled substance abuse (alcoholism, illegal drugs) that would make them unsuitable for the intervention.• Ineligible for pulmonary rehabilitation at their local PR service at the time of randomisation (typically if they had undertaken a course of PR in the last 12 months and there were no new clinical indications for PR [20].• A co-morbidity so severe it would prevent the participant from engaging fully in the intervention/ control e.g.rheumatoid arthritis or osteoarthritis, multiple sclerosis, chronic widespread pain syndrome, previous cerebral vascular event such that the participant would not be eligible for pulmonary rehabilitation.• Participants with moderate/severe cognitive impairment. • In receipt of a psychological intervention primarily directed at helping to manage anxiety or depression in the last 6 months (NB those on antidepressants/ anxiolytics not excluded) or in receipt of a referral for a psychological treatment (e.g.CBT therapy) for management of anxiety or depression.(NB those in receipt of counselling for bereavement or smoking cessation are not excluded).• Participants currently involved in another clinical trial related to COPD (to reduce study participation burden on participants).• Not sufficiently fluent in English to be able to complete the intervention, questionnaires (NB the questionnaires are supervised self-complete, but can be read to participants if necessary, so poor literacy would not exclude individuals who are otherwise sufficiently fluent in English).

Inclusion Criteria -Carers
• Identified by a participant with COPD in the study as a 'particular family caregiver or friend who helps them' and whom they would be happy for us to invite to join the study.

Exclusion Criteria -Carers
• Unable to give valid consent.
• Not sufficiently fluent in English to be able to complete the questionnaires.

Interventions
The designed randomisation ratio is 1.25:1 in favour of the intervention (usual care plus a tailored psychological intervention) compared to the control (usual care).

Intervention
The TANDEM intervention to optimise the potential synergy between the psychological one-to-one CBA intervention and PR.The CBA intervention will precede PR and target individuals' cognitions and behaviours associated with anxiety and depression to decrease psychological morbidity and increase selfefficacy (confidence) and motivation among participants with moderate to very severe COPD to attend and complete PR.

Control
Usual care will follow local arrangements for provision of PR to people with COPD referred to the service, and participants will attend the usual multidisciplinary PR course (including any psychological treatment provided routinely in that service).In agreement with the local service (who may prefer to use their own materials), we will provide the British Lung Foundation (BLF) DVD on living with COPD, and booklets on COPD and pulmonary rehabilitation.Participants will also be eligible for referral to other services, e.g.referral for Improving Access to Psychological Therapies (IAPT) services, at the discretion of their usual healthcare providers.

Outcome measures Primary outcome
The co-primary outcomes are participant depression and anxiety (HADS-D and HADS-A) at 6 months

Other secondary outcomes
Health Economic outcomes (Participant Quality of life (EQ-5D-5L), Client Service Receipt Inventory, and Health Care Resource Use) are addressed in the health economic analysis plan.
Process outcomes are addressed in the process evaluation analysis plan.Sample size calculations are based on two primary outcomes (HADS-A, anxiety, subscale at 6 months, and HADS-D, depression, subscale at 6 months).Based on a two-sided significance level of 2.5% and 90% power, recruiting 153 participants would allow us to detect a difference of 1.7 points on the HADS anxiety subscale, and 1.5 points on the HADS depression subscale (based on a standard deviation (SD) of 4.2 for anxiety and 3.6 for depression [1]): these are equivalent to a standardised mean difference of about 0.4, and are similar to the minimum clinically important difference of 1.5 for HADS in COPD.[2] Due to the clustering effect by therapist in the intervention arm, we increased the sample size.Assuming an intraclass correlation coefficient (ICC) between therapists of 0.01 and 24 participants per therapist leads to a design effect of 1.23, which required increasing the number of participants in the intervention arm to 189 (342 overall).Assuming a dropout rate of 20%, we would require 428 participants overall.This has been rounded up to 430.Using an allocation ratio of 1.25 vs. 1, this would lead to approximately 240 participants in the intervention arm and 190 in the control arm.We have chosen this unbalanced allocation ratio as it will maximise power compared to a 1:1 ratio due to the presence of the anticipated size of the ICC resulting from clustering by therapist in the intervention arm only.

Randomisation procedure
Participants will be randomised to either the intervention or usual care.The allocation ratio will be 1.25:1 ratio in favour of the intervention.Randomisation will be performed by stratification by NHS Trust, and using minimisation within each stratum with a random element of 0.80, [3] balanced for important participant characteristics to ensure treatment groups are well matched at baseline.Stratifying by NHS Trust promotes a comparable distribution of participants across NHS Trusts within the two treatment groups, which is important because although extensive discussion with current applicants, experts and services themselves suggested that PR services should not vary too much within Trusts, they could vary between trusts.Randomisation will be implemented using a central online randomisation service based at Queen Mary University of London.Allocation concealment will be maintained through the use of the centralised service.
The NHS Trusts are as follows, although more Trusts may be added in the future: 3) Modified MRC Breathlessness Scale, with categories: 0-2, 3-4 4) Self-reported smoking status, with categories: smoker, non-smoker (ex-smoker or never smoked)

Baseline characteristics
Baseline characteristics and questionnaires will be summarised for each treatment group by the mean and standard deviation (SD) or median and interquartile range for continuous variables, and the number and percentage for categorical variables.See Table 1, Table 2, Table 3, and Table 4 in Appendix 4.

Adherence to treatment
For our analysis, a participant in the intervention arm is considered to have completed CBA (typically 6-8 sessions) if they complete 2 or more sessions (as per protocol, completion of two sessions considered minimum effective dose of the intervention).A participant in either arm of the study is considered to have completed PR if they complete 75% or more of their scheduled PR sessions.See Table 97.

Information for CONSORT flow diagram
See Appendix 3 for a dummy CONSORT flow diagram.

General analysis principles
Analyses will follow the intention-to-treat (ITT) principle.This requires that all participants be included in the analysis according to the treatment group to which they were randomised, regardless of any departures from randomised treatment.[4] Anyone identified post-randomisation as having been ineligible for the trial at the time they were randomised is not considered a 'participant' in this sense, and will be excluded from all analyses (a count of these will be provided in the CONSORT flow-chart).Where it is not possible to follow up participants, we will handle missing data by including all those with a recorded outcome.[5] A secondary analysis will estimate the complier-average causal effect (CACE), based on adherence as defined above.This is the intervention effect in participants who would adhere to the intervention, and is estimated in a way that respects randomisation (in this regard it is superior to a per protocol analysis).• The number of participants included in the analysis, by treatment group; • A summary measure of the outcome, by treatment group (e.g.mean (SD); • A treatment effect (difference in means) with a 95% confidence interval; • A two-sided p-value For all analyses, a significance level of 5% will be used, except when the Hochberg procedure is applied to account for there being two primary outcomes.
All analyses will account for the partially clustered design of the study, due to the clustering effect by facilitator in the intervention arm only.Each participant in the intervention arm will be defined as belonging to a cluster, defined by which facilitator they belonged to.It is possible that the facilitator could change for a participant, for example if a facilitator withdraws and a new facilitator is assigned to a participant.In such scenarios, for analysis purposes we will consider that the participant is clustered within the facilitator for which they have had the majority of their sessions.If they had equal amounts of sessions under multiple facilitators, we will take the first of such facilitators.The clustering effect by facilitator in the intervention arm will be modelled using a partially nested mixed-effects model, which confines the random effect for cluster to the intervention arm only.If we write out the model for the two levels of treatment, this essentially amounts to a random intercept for each cluster in the intervention arm and one intercept for the unclustered control arm.[7,8] In order to run the model in Stata, we treat each participant in the control arm as a single cluster, and allow the residual variance to be different in the intervention and control arms.[7] All analyses will also account for the correlation between outcomes at 6 and 12 months using a random effect for participant.This approach will provide unbiased estimates even if some participants only provide data at one of the two time points, under the missing at random assumption implied by the model.We fit a heteroscedastic model, allowing for different residual level errors in the two treatment arms since we might expect participants in the intervention arm to vary in a different way to those in the control arm.[7,8] The model will be estimated using restricted maximum likelihood (REML).Treatment arm, time point (month 6 or 12), and the interaction between treatment arm and time point will be included in the model as fixed factors.
All analyses will adjust for the outcome measured at baseline whenever possible.Moreover, analyses will reflect the design of the study, and so stratification and minimisation variables will be adjusted for.[9] These covariates will not be interacted with time point.Continuous covariates will be fitted for the HADS-A and HADS-D screening scores.Although categories were used for HADS-A and HADS-D during the minimisation, we avoid unnecessary categorisation of the covariates for the analysis as this should increase power.[10] Continuous covariates will be assumed to have a linear relationship with the outcome.Binary covariates will be fitted for the baseline degree of breathlessness (categories: 0-2 and 3-4) and baseline smoking status (categories: smoker and non-smoker (ex-smoker/never smoked)).We also adjust for NHS Trust as a fixed categorical variable.Due to the large number of NHS Trusts, one could fit a random effect for Trust, but this would result in a complex (four-level) mixed effect model with concerns about fitting due to the sample size and so in this situation a fixed effect is preferable.Moreover, the other stratifiers are nested within Trust.Furthermore, when there are a large number of participants per centre (25 or more, which we expect here), random and fixed effect perform equally well in terms of coverage, power and efficiency.[11,12] See Table 7 for how we will present the main results for the primary and secondary continuous outcomes.

Binary outcomes
The only binary secondary outcome is smoking status at 6 and 12 months (current smoker vs non-smoker).Decreased smoking cessation in the intervention arm is psychologically plausible with the Tandem intervention (increased self-efficacy around condition management increasing likelihood of attempting and succeeding in quitting).We will attempt to follow an analysis strategy similar to that outlined above for continuous outcomes, but using mixed logistic regression in place of mixed linear regression, and introducing any simplifications as required to produce an effect estimate if there are problems with model convergence (see strategy in next section).There may not be a great deal of movement in this outcome from baseline making it more of a challenge to analyse than other outcomes.It is also of less direct interest than other secondary outcomes, and a simpler analysis may be an acceptable trade-off.
See Table 8 for how we will present the results.
Other analyses involving binary outcomes, such as CBA intervention attendance and completion rates, and PR attendance and completion rates, are discussed in Section 6.

Model convergence issues
If a model fails to converge, the following strategy will be employed, with changes considered in the order presented: 1 Remove the correction allowing for a small number of clusters (Satterthwaite correction -see model specification below) 2 Remove the minimisation covariates 3 Remove the baseline assessment of outcome as a covariate 4 Split the two time-points into two separate models -i.e.remove the fixed effect for time and the random effect for participant 5 Fit a homoscedastic model -i.e. one overall residual variance (independent residual structure) rather than separate variances estimated for the two treatment groups (could be one of two alternatives -either assuming the control arm is a single 'cluster', or that each individual in the control arm is a separate 'cluster') 6 Remove the random effect for facilitator

Missing data for baseline covariates
We do not expect missing data for any of the baseline covariates for the primary analysis.It is possible that there will be a small amount of missing data for the secondary outcomes measured at baseline.In this case, missing data for baseline covariates to be included in the analysis model will be accounted for using mean imputation.[13] Missing data for outcomes For outcomes that are measured at multiple time points during follow-up, we have based our analysis strategy on that proposed by White et al 2011.[5] To deal with incomplete data (i.e. when participants have missing data at one of the follow-up time points) we will: 2. Perform a main analysis of all observed data that are valid under a plausible assumption about the missing data

3.
Perform sensitivity analyses to explore the effect of departures from the assumptions made in the main analysis

4.
Account for all randomised participants, at least in the sensitivity analyses For the main analyses (point 2), we will include all participants with at least one post-randomisation assessment (i.e. if the relevant outcome is recorded for at least one follow-up time point) in the analysis.Participants with missing outcome data at both 6 and 12 months will be excluded for this analysis.The mixedeffects model adjusted for baseline covariates assumes that the data are Missing at Random (MAR).[14] Modelling of the observed data in this way is a principled method to deal with missingness, as information is 'borrowed' from other clusters.This strategy of analysis has been widely recommended in the presence of missing outcome data.For outcomes that consist of several items combined to create a score, we expect most participants will either complete all or none of the items.Only participants who completed all of the questions which form the score at either 6 or 12 months will be included in the primary analysis.
We perform sensitivity analyses for the primary outcomes to assess the robustness of our primary analysis to the missing data assumptions (point 3) and account for all the participants analysed, including those lost to follow up or withdrawn (point 4).See section 5.6.

Analysis of co-primary outcomes
We will analyse the co-primary outcomes separately.This is equivalent to fitting a joint model in the case of no missing data.A joint model would be more efficient in the case where one outcome is missing but the other outcome is not.However, a joint model is more computationally complex and it is unlikely that participants would complete the HADS-A questions but not the HADS-D, and vice versa.
A heteroscedastic partially nested mixed-effects model will be fitted for HADS-A and HADS-D, as follows: where the clusterid represents the facilitator for each participant in the intervention arm and each individual participant in the control arm (see section 5.4).
With mixed regression modelling there is a risk that the type I error rate will be inflated when the number of clusters is small, and a variety of corrections have been proposed.We will use the Satterthwaite method (the 'dfmethod(sat)' option in Stata), as recommended by Candlish et al. [8,16,17] We will use a Hochberg procedure to analyse the two primary outcomes.[15] The Hochberg procedure states that if either outcome has a p-value <0.025 then that outcome is statistically significant; additionally, both outcomes are significant if both p-values are <0.05.

Complier Average Causal Effect (CACE) analysis for co-primary outcomes
As a secondary analysis we will estimate the Complier Average Causal Effect (CACE) for each co-primary outcome, with compliance defined as attending at least two CBA sessions.The CACE analysis will be performed with a latent class modelling approach, using the gllamm command in Stata (Generalised Linear Latent & Mixed Models; http://www.gllamm.org/books/cace.html).This will assume the same mixed model as in the intention-to-treat analysis, above, with repeated assessments at 6 and 12 months, clustering in one arm and heteroscedasticity between the arms.

Missing data
For the primary analysis, we do not expect missing data for any of the baseline covariates because they are all randomisation variables.However, there may be some missing outcome data.In the primary analysis, participants who complete all of the questions that form the score at either 6 or 12 months are included; participants with missing outcome data at both 6 and 12 months are excluded.This mixed-effects model adjusted for baseline covariates assumes the data are MAR.We will perform the following sensitivity analyses to assess the robustness of our primary analysis to different assumptions regarding the missing data.These sensitivity analyses will be performed for the coprimary outcomes (HADS-A and HADS-D at 6 months):

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• A complete case analysis which assumes data missing at six months is missing completely at random (MCAR) • An analysis in which participants with partially incomplete HADS-A or HADS-D have missing items imputed • An analysis which assumes that data missing at six months is missing not at random (MNAR) For the complete case analysis, we will fit the primary analysis model but only include participants with fully recorded data at six months.Participants who did not complete all components of the HADS-A or HADS-D questions respectively at six months will be excluded from the corresponding analysis.
For the second analysis we will follow the 'half-rule' suggested by Bell and colleagues, in which missing HADS items are imputed using the relevant subscale mean, as long as at least half the items in the subscale are non-missing.[18] For the third analysis, we will assess the primary outcomes under a range of MNAR scenarios.This will be done following the simple approach proposed by White et al 2007.[19] We use the formula ∆ = ∆CC + Y1P1 -Y2P2, where ∆ is the treatment effect under the MNAR scenario, ∆CC is the treatment effect from the complete case analysis on six month data above, Y1 and Y2 are the assumed six month mean responses for participants with missing data in treatment groups 1 and 2 respectively, P1 and P2 are the proportion of participants who were excluded from the six month analysis in groups 1 and 2 respectively, and groups 1 and 2 represent the intervention and control groups respectively.The standard error for ∆ is assumed to be approximately equal to the standard error for ∆CC.Y2 will be varied for both outcomes between -10, -5, -1.5, 0, 1.5, 5, and 10.Negative values indicate the participant got less anxious/depressed at 6 months, positive values indicate they got more so, and a value of 0 indicates there was no change from baseline.For each value of Y2, Y1 will be set to Y2 -5, Y2, and Y2 + 5.For example, for Y2 = 10 and the HADS-A outcome, this would indicate an assumption that participants in treatment arm 2 (the control arm) who were lost to follow-up at 6 months, had gained 10 points on the HADS-A subscale on average at 6 months.Y1 would vary between 5, 10, and 15, indicating the assumption that participants in treatment arm 1 (the intervention arm) who were lost to follow-up had gained 5 points on the HADS-A subscale on average at 6 months (5 points less than those in the control arm), 10 points (the same amount as those in the control arm), or 15 points (5 points more than those in the control arm).It is possible that the value of ∆ that we obtain may be implausible if it goes outside the score range of 0-21.In such cases we will truncate ∆ by the scale boundary.We will note any "tipping point" -the value the treatment effect in the non-responders would need to be to change conclusions.
Finally, we will compare the distribution of baseline characteristics of people included in the primary analysis model and those missing the primary outcome at both 6 and 12 months.Moreover, we will present the characteristics of people who have missing follow-up data because they died.

Inclusion criteria
We will perform a sensitivity analysis to assess the impact of including participants in the analysis who have less room for improvement during follow-up.The inclusion criteria state that participants must have a score of 8 or more on either the HADS anxiety or depression subscale (but not necessarily both), so some participants may have a score of <8 on one of these subscales and therefore have less room for improvement PCTU_TEM_ST_02 Tandem Statistical Analysis Plan template V 3.0 Document version 2.0 during follow-up.We will assess the impact of including such participants, by repeating the primary analyses for HADS-A and HADS-D but excluding participants who have a score of <8 on the HADS-A and HADS-D subscales respectively.The anxiety and depression subscales of HADS are strongly associated, [20] meaning that it is unlikely that many participants have scores a lot lower than 8 on either subscale.

Time to pulmonary rehabilitation
We will assess the impact of any difference in time from baseline to attending PR in the intervention and control groups.We will summarise the time to PR in the two groups, presenting the mean (standard deviation) and the median (interquartile range).As a sensitivity analysis to the analysis of co-primary outcomes described above we will repeat the primary analysis model but with time to PR as an additional covariate.

Internal pilot
We will perform a sensitivity analysis excluding the internal pilot participants from the primary analysis, to assess the potential impact of a 'learning effect' in the pilot.For example, it is possible that the delay between completion of training and the start of intervention delivery in the internal pilot may have resulted in the treatment looking less effective in the pilot than later participants.

Allocation ratio
We know that there was a problem with the randomisation system leading to the allocation ratio being different in different periods of the trial.Specifically, over the first 69 randomisations (randomisation period 1) the observed allocation ratio was around 1.25:1 as expected; over the next 70 randomisations (randomisation period 2) the observed allocation ratio was around 5:1; this deviation from the expected allocation ratio led to a Corrective Action and Preventive Action plan that included migrating the randomisation system to a new platform, and for the remainder of randomisations (randomisation period 3) the observed allocation ratio was around 1:1 as was specified on the new platform in order to return the overall allocation ratio to a figure closer to 1.25:1.We will fit the same primary analysis model as specified in Section 5.5 but with randomisation period as an additional covariate.We will also look at the measured characteristics of participants to see if there is evidence that they are different in each time period, although Tandem is a fairly rapidly recruiting trial and we do not expect this to be the case.We will also report the balance of minimisation factors in each NHS Trust -see Table 5.

Covid 19
In late March 2020 the UK government imposed a "stay at home" order in light of the spread of COVID-19.
Recruitment was due to be stopped on 30 March 2020 but curtailed about 11 days earlier due to COVID-19.Nevertheless, 427 out of 430 (target) patients were successfully recruited to the study.
We will perform a sensitivity analysis to assess the impact of the COVID-19 pandemic on the results of the co-primary outcomes.This assessment will be undertaken by splitting data in the following two ways: 1. whether data were collected before or after 19 March 2020, which is the assumed cut-off date for pre-pandemic and during pandemic outcomes.2. whether the mode of intervention delivery was i) fully face-to-face or, ii) partially or fully via remote sessions.
The aim of this two-fold splitting is to explore several mechanisms through which COVID 19 may have impacted the trial outcomes.
For each way of splitting the data we will perform two analyses: a) a sensitivity analysis repeating the primary analysis model but with trial period as an additional covariate (i.e. an indicator variable that specifies for each outcome assessment in the analysis whether the period should count as being before or after the cut-off); b) an analysis to see whether the effect of the intervention is modified by trial period, performed by adding an interaction between the treatment effect at 6 months and trial period, and an interaction between the treatment effect at 12 months and trial period, to the analysis model in (a).

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We will also look at measured baseline characteristics of participants to examine any evidence for differences between trial periods., and Table for how we will present the results of the sensitivity analyses for the coprimary outcomes.

Participant Depression (HADS-D) at 12 months
This outcome is included in the same model as the HADS-D primary outcome.

Participant Anxiety (HADS-A) at 12 months
This outcome is included in the same model as the HADS-A primary outcome.

Participant Depression (BDI-II) at 6 and 12 months
These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline BDI-II as an additional covariate in the model.

Participant Anxiety (BAI) at 6 and 12 months
These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline BAI as an additional covariate in the model.

Participant Smoking status at 6 and 12 months
We will attempt to analyse smoking status using a mixed logistic regression model similar to the mixed linear regression model for the primary outcomes, though we anticipate a greater risk of model convergence issues in this case and some simplification to the analysis strategy may be required.See Table 8.

Participant Respiratory Health-related quality of life (SGRQ) at 6 and 12 months
Separate models will be fitted for the three component scores (symptoms, activity, impact) and the total score.These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with the relevant component score or total score for SGRQ at baseline as an additional covariate in the model.

PCTU_TEM_ST_02 Tandem Statistical Analysis Plan template V 3.0 Document version 2.0 Participant Illness perceptions about COPD (B-IPQ) at 6 and 12 months
There are 8 items, with each item scored from 0-10.Each item of the Brief IPQ assesses one dimension of illness perceptions (see Appendix 2).Separate models will be fitted for the 8 scores.These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with the relevant component score for B-IPQ at baseline as an additional covariate in the model.
Participant Social engagement (heiQ) at 6 and 12 months These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline heiQ as an additional covariate in the model.

Participant Social functioning (Time Use Survey) at 6 and 12 months
We will analyse the time (minutes) spent doing activities over the last 4 days.This outcome will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline time (minutes) spent doing activities over the last 4 days as an additional covariate in the model.Time spent doing activities over the last 4 days will be assumed to have a linear relationship with the outcome.

Carer Burden Interview (ZBI) at 6 and 12 months
These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline ZBI as an additional covariate in the model.

Carer Mental Well-being (WEMWBS) at 6 and 12 months
These outcomes will be analysed using the same model as the primary outcomes at 6 and 12 months, with baseline WEMWBS as an additional covariate in the model.

Interim analyses
There are no formal interim analyses planned.The Data Monitoring Committee will see unblinded interim data summaries in closed session.These closed reports are produced by a statistician independent of the study team.

Blinding of the statistical analysis
Analysis cannot be blinded because of the allocation ratio.As far as possible all cleaning and checking of the data will be done before the statistician has access to the allocation codes.

Analysis software
The analysis will be carried out using Stata version 14 or newer.R version 3.6.1 or newer may be used if necessary.The software and version number used will be referenced with any analysis write up.

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Tandem Statistical Analysis Plan template V 3.0 Document version 2.0

Data completeness
We will report on completeness of data on questionnaires.See Table 6.

Compliance with the intervention
We will report on CBA intervention attendance and completion rates, and PR attendance and completion rates.See Table 97 -CBA and PR attendance and completion.
Section 5.2 outlines our definitions of completion of CBA and PR.We will calculate the rates as follows: CBA intervention attendance rate = o/p, where o = number who attended/received at least one CBA session p = number allocated to intervention CBA intervention completion rate = q/o, where q = number who completed CBA o = number who attended/received at least one CBA session The number who attended at least one CBA session, o, can be obtained from the number of patients with a session number for the "SESSNO" variable for at least one session (and without an entry for "FAILDELIV"failure to deliver).The number who completed CBA, q, can be obtained from the number of patients who attended at least two CBA sessions.Both these variables are recorded in the 'CBA Facilitator -CBA session contact log' section of the database.The number allocated to the intervention, p, can be obtained from the randomisation database.
PR intervention attendance rate = r/s, where r = number who attended/received at least one PR session s = number referred and deemed suitable to attend PR PR intervention completion rate = t/r, where t = number who completed PR r = number who attended/received at least one PR session The number referred to attend PR, s, can be obtained from the number of patients with a value of one or more for the "NUMBER OF PR SESSIONS SCHEDULED " variable.The number who attended at least one PR session, r, can be obtained from the number of patients with a value of one or more for the "NUMBER OF PR SESSIONS COMPLETED " variable.The number who completed PR, t, can be obtained from those with a value of 0.75 or more for the ratio of "COMPLPR" to "SCHEDPR".All these variables are recorded in the 'collection of PR attendance and completion data' section of the database.

Safety analyses
We will report on adverse events and serious adverse events.See Table 19

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Examine the clinical effectiveness of the CBA intervention on clinical outcomes compared to usual care (the offer of pulmonary rehabilitation (PR) alone).2) Examine the process outcomes.

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Sample size and randomisation Sample size calculation Intervention (usual care plus a tailored psychological intervention): 240; Control (usual care): 190