Identification of subgroup effect with an individual participant data meta-analysis of randomised controlled trials of three different types of therapist-delivered care in low back pain

We did a systematic review to identify potential moderators to apply to our dataset. The studies identified in this review formed the basis of the trials we sought to include in this study [10]. In this review MEDLINE, EMBASE, Web of Science and Citation Index and Cochrane Controlled Trials Register (CENTRAL) databases were searched using the terms ‘low back pain’ combined with ‘trial’, ‘observational’, ‘cohort’ and ‘prospective studies’. Two independent reviewers assessed risk of bias based on these criteria: method of randomisation, allocation concealment, incomplete outcome data, selective outcome reporting, and other sources of bias. We searched the original search output for randomised control trials that had interventions being delivered by a therapist and had a sample size > 179. We invited investigators of the trials identified to share trial data with us. We focussed on recently published larger trials to ensure we included higher quality studies, where data would be more likely to be available. Including large numbers of small studies would have substantially increased work needed to prepare data for inclusion in our database. Having said this we were offered data from a few smaller studies which we decided to include to improve the statistical power of our analysis. Full details of our approach to obtaining data and developing and managing the repository are published elsewhere [8].

As trials had a range of therapist-delivered and control interventions we grouped this to allow meaningful analysis. Using a similar approach to the American Pain Society/American College of Physicians guidelines of grouping non-pharmacological interventions [11], groups were: control (non-active usual care), sham control (sham acupuncture, electrotherapy, advice/education, mock transcutaneous electrical nerve stimulation), active physical (exercise and graded activity), passive physical (individual physiotherapy, manual therapy, acupuncture) and psychological (advice/education, psychological therapy) [8, 9].

As trials had different follow-up times, we classified follow-up into short- (2 and 3 months), mid- (6 months) and long-term (12 months post randomisation). We classified the 32 patient reported outcome measures (PROMs) used into physical disability, pain, psychological distress and non-utility quality of life. As has previously been shown, LBP disability measures cannot be mapped into a single outcome [12], analyses were therefore only performed on measures common to more than one trial. We have presented the response for each clinical outcome measurement as the change from baseline to the follow-up time point with a positive score representing an improvement. Individual items (if available) were used to obtain the composite score otherwise, the original individual composite scores were used.

We summarised categorical data as frequency and percentage, and continuous data as mean and standard deviation (SD), by treatment arm; control (non-active usual care and sham) and intervention (active physical, passive physical, psychological, and combination). Our main analyses were based on complete case analysis with missing data due to non-responders or withdrawals not imputed. Analyses were performed on IPD from at least two trials so as not to replicate original analyses.

We identified potential moderators in two ways. Firstly, from our systematic review identifying potential treatment moderators (factors measured pre-randomisation indicating who benefits most and least from a treatment) [10]. Secondly, including IPD from all RCTs in a single mixed-effects meta-analysis model for each follow-up time with moderators declared statistically significant at the two-sided 5% or weakly significant at the two-sided 20% level [13].

We applied two approaches to identification of subgroups: Recursive Partitioning (RP) [14] and Adaptive Refinement by Directed Peeling (ARDP) [15]. Both aim to identify subgroups of participants with treatment effect larger than for other participants, by considering subgroups defined by ranges of values for sets of moderators. The RP method creates subgroups by successively splitting the population to build up a subgroup. It utilises a splitting criterion to create binary splits of the covariate space thus forming a tree-like structure. This splitting criterion isthe p-value of the subgroup effect (treatment by covariate interaction) which is estimated using a mixed-effects model to account for the between trial heterogeneity.

The ARDP method starts with the whole population then removes parts of it, thereby increasing the observed treatment effect in the remaining subgroups. The criterion for optimisation is based on the interaction between treatment and subgroup which allows for between-trial heterogeneity. This method splits categorical covariates using each of its categories, for example, sex would be split into male and female. Therefore, categorical covariates with three or fewer categories would cause the method to remove a large proportion of participants at each stage, an unappealing feature. Covariates with three or fewer categories were not included in this analysis.

To establish proof of principle for our novel methods we first ran our analyses on the overall dataset before running our main analyses for the pairwise comparisons of active physical, passive physical and psychological treatments against control. It is these three distinct comparisons that are the clinically outputs from this study. We present our methodological steps in some detail to introduce the reader to our methodological approach.

We collected data from 9328 participants from 19 trials (Tables 1 and 2). We identified three broad treatment types within the data repository for which we wish to explore potential moderators; (i) active physical, ii) passive physical, iii) psychological treatments. Control arms included non-active usual care and sham intervention.

There were 5349 (57%) females with similar ratios of females in control and intervention arms. The average age was 49 years (standard deviation, SD, 14). The age range is slightly different across treatment arms due to different inclusion criteria of the trials [9].

The most frequently used PROM for physical disability was the Roland Morris Disability Questionnaire (RMDQ), (m = 14 trials, n = 4710 participants). This was followed by the disability score domain in Chronic Pain Grade (CPG-DS) (m = 4, n = 3328), the Hannover functional ability questionnaire for measuring back-pain related functional limitations (FFbHR) (m = 3, n = 4176) and the patient specific functional scale (PSFS) (m = 3, n = 667) (Additional file 1: Appendix 1). The physical disability, functional limitation and pain mean scores between control and intervention arms at baseline were very similar. The mean RMDQ score was 9.9 (SD, 5.1; where a maximum score of 24 was worst), CPG-DS was 50.2 (SD, 22; where a maximum score of 100 was worst), and FFbHR was 57.6 (SD, 20.5; where a maximum score of 100 was best). Most trials measured psychological distress but the wide variety patient reported outcome measures (PROMs) made direct comparisons impossible.

In our overall one-step meta-analysis (MA) intervention was better than control in improving most outcomes in the short-term (Fig. 1 & Supplementary Table 1). As treatment effects at mid and long-term were generally not statistically significant, we only explored potential moderators for short-term follow-up.

We included potential effect moderators identified from our systematic review [10] and one-step MA in the mixed effects model. In our overall short-term analysis, we found few potential moderator effects (Fig. 2 & Supplementary Table 2). Overall, the baseline value of a measure moderated treatment effects on that measure; FFbHR at baseline moderates the effect on FFbHR, physical component scale (PCS) at baseline moderates the effect on SF-12/36 PCS, and mental component scale (MCS) at baseline moderates the effect on SF-12/36 MCS. Age, gender, LBP disability and severity (FFbHR, RMDQ, Pain and PCS), psychological state (MCS, anxiety, catastrophising and coping) were at least weakly significant in one or more moderator analysis and were considered for further subgroup analysis.

Analyses included between 1339 and 5208 people (from two to seven trials; Additional file 1: Appendix 2). We identified subgroups for three of the short-term outcome measures; FFbHR, SF-12/36 MCS and SF-12/36 PCS.

Those with more back pain disability at baseline (FFbHR≤54.2) benefitted more from any therapist-delivered intervention at short-term follow-up than those with FFbHR> 54.2 with treatment effects of 11.3 (95% confidence interval, CI, 9.38 to 13.23) and 6.6 (95% CI, 5.46 to 7.78) respectively, when measured by the FFbHR (Fig. 3). However, those with greater back pain disability (FFbHR≤54.2) and younger (age ≤ 60) gained the greatest benefit on the FFbHR outcome at short-term, with a treatment effect of 13.2 (95% CI, 10.56 to 15.77) compared to those with FFbHR≤54.2 and age > 60, for whom the treatment effect was 8.1 (95% CI, 5.47 to 10.80) (Fig. 3). For the short-term SF-12/36 MCS outcome, those with greater baseline psychological distress gained most benefit (3.5; 95% CI, 2.62 to 4.30) (Fig. 3) from any therapist-delivered intervention. For the short-term SF-12/36 PCS outcome, females with less psychological distress (MCS > 50.9) gained most benefit (4.7; 95% CI, 3.67 to 5.78) or those with less psychological distress (MCS > 50.9) and worse physical disability (PCS ≤ 40) gained more benefit from any therapist-delivered intervention (4.9; 95% CI, 3.96 to 5.82) (Fig. 3).

Analyses included between 496 and 3879 people (from two to seven trials; Additional file 1: Appendix 3).

Analyses included between 1365 and 5208 people (from two to eight trials; Additional file 1: Appendix 2).

Categorical covariates such as gender and psychological states with three categories (anxiety, catastrophising and coping) were excluded from subgroup identification with ARDP method because a split on these categorical covariates would lead to a large proportion of participants being removed. Additional file 1: Appendix 7 shows the trajectory plot for the interaction treatment effect against the size of the subgroup for short-term (a) FFbHR, (b) RMDQ, (c) Pain, (d) PCS of SF-12/36, (e) MCS of SF-12/36, and (f) EQ-5D. Treatment effects generally increased as subpopulations get smaller but the strong fluctuations for RMDQ (Additional file 1: Appendix 7, figure (b)), Pain (Additional file 1: Appendix 7, figure (c)) and PCS (Additional file 1: Appendix 7, figure (d)) suggest that no subgroup would gain greater improvement in these outcomes.

Table 3 shows the thresholds for selected sizes of the subgroup for the short-term FFbHR found in Additional file 1: Appendix 7, figure (a). The average treatment effect on the short-term FFbHR of approximately 90% of the population (PCS < 48 and MCS < 72) was 8.5. The average treatment effect increased by 8 units to 16.8 in a subpopulation with FFbHR < 29, PCS < 68 and MCS < 57. However, the proportion of participants with such great improvement is very small (approximately 10%). Similarly, 10% of the population (PCS < 29 and MCS < 51) had a very large average treatment effect on the short-term SF-12/36 MCS compared to 90% of the population (PCS < 48 and MCS < 72); 6.0 units compare to 2.2 units (Additional file 1: Appendix 8), suggesting that participants with more psychological distress would gain greater improvement. It is interesting that in the construction of subgroups, the disability scale, FFbHR, did not seem to be an important covariate whereas the functional scale of the SF-12/36 PCS suggested that those with poor physical status would gain greater improvement. Population with low PCS and high RMDQ at baseline (corresponding to poor disability and physical status) also had greater improvement on short-term health utility measured by EQ-5D (Additional file 1: Appendix 9).

Since we started this work, an RCT testing the STarT Back Screening Tool for risk stratification, which had a positive result and was published and included in NICE guidance [36]. This compared standard care to a risk stratification tool that allocated participants to one of three treatment packages delivered by specially trained physiotherapists. The content of the physiotherapy and differences between intervention and control physiotherapists may have contributed to the effect size. The treatment effect moderation of the STarT Back tool was not tested. This trial, therefore, does not materially affect our conclusions.

Further developments in risk stratification tools continue despite challenges of accuracy and application reported by therapists [37]. Some argue for a more multidimensional stratification approach, although our results have not consistently supported this [38]. There are other approaches that might be used to explore these data to identify how participant characteristics might moderate response to different treatments approaches. This is beyond the scope of this current piece of work.

In 2019, after we had completed our work, an IPD meta-analysis of exercise therapy for LBP was published [7]. This work included data from 3514 people from 27 trials. The focus was on exercise interventions only, limiting analysis to moderation effects of single variables, and the inclusion of larger numbers of smaller trials (average size 130) makes this work distinctly different from the work presented here. The authors found some exploratory evidence that those with less physically demanding jobs, or who use pain medication are more likely to benefit from exercise therapy than other treatments in the short term. Lower BMI was also reported to improve outcomes from exercise. In our work, we have focused on therapist-delivered interventions more broadly including active physical, passive physical and psychological treatments rather than just exercise therapy. This has allowed us to include some large high quality trials giving us a much larger overall dataset. The challenge of small low quality studies being included remains.

A 2020 IPD meta-analysis of acupuncture for chronic pain included data from 20,827 people from 39 trials and did not find a subgroup responding exceptionally better to acupuncture [39]. Similarly, an IPD meta-analysis of spinal manipulative therapy (SMT) for chronic low back pain did not find a subgroup that would gain greater benefit from SMT compared to other treatments [40].

Despite our large initial dataset, many analyses used only a small subset of the data because we were unable to pool outcomes measuring the same domain to a common scale [12]. We are confident, however, that the same domain is being measured in each trial.

We did not do a risk of bias assessment for included studies. This would have been important for a review reporting overall treatment effects; and appropriate tools are available. However, for an IPD meta-analysis of this nature exploring sub-group effects we are not aware of any tool to assess risk of bias specifically in moderation effects.

The decision to group trials into active physical, passive physical, psychological, sham and control could be questioned but was necessary for meaningful analyses. Our approach was very carefully considered and agreed by the research and lay team.

For our analyses, we used the mental and physical component scores of the SF-12/36 rather than their eight domain scores. This because we considered these were more clinically relevant as outcomes and to avoid further complicating our analyses, and their interpretation, by adding additional variables. We cannot exclude that an analysis using the individual domain scores as explanatory variables rather than the component scores might have produced a different outcome.