In much of orthopedics and rehabilitation, two treatments with clearly different early results end up in the same place. Plates and screws beat external fixators for ankle fusion at three months, but the difference is gone at one year (Evaluation of the effectiveness of ankle arthrodesis options). Internal fixation of a broken wrist restores grip faster, but surgical and non-surgical patients look alike at one and five years (Distal radius fracture: review). Structured rehabilitation after COVID-19 shortens lung recovery from twelve weeks to four, and the groups meet by six months (Pulmonary Rehabilitation Accelerates the Recovery of Pulmonary Function in Patients With COVID-19). Papers usually explain this pattern, which we call convergence, as "biology reaching its ceiling." Nobody has tested that explanation. An equally plausible account is that the arm that starts behind catches up psychologically: mood and coping improve, and that improvement drives later physical function. A third, more worrying account is that a real lasting physical advantage of one treatment is cancelled out by a psychological cost of the same treatment. In that case the averages look equal while the mechanisms do not.
We propose to estimate how a shrinking treatment gap breaks into two parts. One part is a shrinking direct effect, meaning the effect that does not run through mental health. The other is a shrinking indirect effect that runs through mental health. We would do this in a population trauma registry with repeated follow-up, using estimators that remain valid when early physical recovery both results from treatment and confounds later psychological state. In short, convergence becomes a quantity with a mechanism split and a confidence interval, not just a description of two curves meeting. That split determines whether "equal long-term outcomes" justify the cheaper treatment.
Core Claim
Let $A$ be a treatment contrast, $M_t$ a psychological state measured at follow-up wave $t$, $L_t$ the physical recovery state at wave $t$, and $Y_t$ functional outcome at wave $t$. At each wave the overall effect can be written as an interventional direct effect plus an interventional indirect effect. "Interventional" means the mediator is set to a random draw from its distribution under each treatment. This version stays identified when $L$ is affected by treatment and also confounds $M$ and $Y$, which the classical "natural" effects do not. Convergence between an early wave $t_1$ and a late wave $t_2$ then decomposes exactly as
$$ \underbrace{\mathrm{TE}(t_1)-\mathrm{TE}(t_2)}_{\text{gap closure}} \;=\; \underbrace{\mathrm{IDE}(t_1)-\mathrm{IDE}(t_2)}_{\text{direct decay}} \;+\; \underbrace{\mathrm{IIE}(t_1)-\mathrm{IIE}(t_2)}_{\text{psychological change}}, $$
where TE is the interventional overall effect, IDE the interventional direct effect, and IIE the interventional indirect effect through $M$.
Three hypotheses make different predictions. Under "biological ceiling," IDE decays toward zero and IIE stays small throughout. Under "psychological catch-up," IIE accounts for a substantial share of gap closure. Under "masked divergence," IDE stays clearly nonzero at $t_2$ while IIE of opposite sign cancels it. The new contribution is the estimand: a decomposition of the change in effects across waves, with joint inference over waves, applied to convergence. The combination of estimators that makes it identifiable in a retrospective registry with attrition is the means, not the claim.
Where This Sits
Three bodies of work supply the components, and none answers this question.
The convergence studies motivate the gap. Beyond the examples above, they include rotator-cuff repair techniques that converge after two years (All-Arthroscopic versus Mini-Open Repair of Small to Large Sized Rotator Cuff Tears: A Meta-Analysis of Clinical Outcomes) and 3D-printing-assisted acetabular fixation that improves surgery but not long-term function (Efficacy and safety of three-dimensional printing technology assisted open reduction and internal fixation versus conventional surgery in the treatment of acetabular fractures: a meta-analysis of randomized controlled trials). All of them compare group means at fixed milestones and measure no mechanism.
The closest empirical anchor is the Victorian State Trauma Registry analysis of 4,368 survivors (Predictors of Long-Term Outcomes Following Major Trauma: A Population-Based Study). It found that physical health (the SF-12 physical summary) improves between 6 and 12 months and then plateaus, while mental health (the SF-12 mental summary) is flat in year one and improves between 12 and 24 months. This timing is exactly what the catch-up hypothesis needs. That paper used random-effects regression, did no mediation analysis, did not address time-varying confounding, and assumed attrition was ignorable even though only 69% completed all three interviews.
Psychological mediation research supplies the hypothesis that mental states transmit effects in sequence. Examples include the chain from social exclusion through loneliness and self-control to smartphone addiction (Exploring the relationship between social exclusion and smartphone addiction: The mediating roles of loneliness and self-control) and the chain from sleep reactivity through emotion regulation to depression (Sleep Reactivity and Depressive Symptoms Among Chinese Female Student Nurses: A Longitudinal Mediation Analysis). Resilience mediating surgical anxiety (The relationship between uncertainty and acute procedure anxiety among surgical patients in Chinese mainland: the mediating role of resilience) is the clinical case closest to ours. These studies constrain our design more than they supply a method. They mostly use regression-based path models that condition on intermediate variables, and that conditioning is exactly what produces bias when an earlier physical state is a common cause of later mood and later function.
The method comes from three causal-inference papers, each missing one piece. General targeted machine learning for modern causal mediation analysis provides doubly robust mediation estimators that handle a treatment-affected confounder of mediator and outcome. Its implementation is the crumble package, and it was applied to 1.7 million Medicaid patients, where it attributed 80% of a 1.31% increase in opioid-use-disorder risk to pain-management practices. Its outcome is a single scalar, and it does not compare effects across waves. Doubly-Robust Functional Average Treatment Effect Estimation estimates whole effect curves with simultaneous confidence bands, but only total effects. Estimation and Inference for the Mediation Effect in a Time-varying Mediation Model shows that mediation can rise and fade: the negative-affect pathway in smoking cessation peaked in week one. It offers only pointwise intervals and no adjustment for time-varying confounding. We reuse the first paper's estimator, borrow the second's idea of joint inference across time, and treat the third's finding as a check that our method can detect a mediation effect that changes over time.
Research Program
The setting is the Victorian State Trauma Registry. Its 6-, 12- and 24-month telephone follow-ups record the Glasgow Outcome Scale-Extended (a 1–8 functional recovery score), the SF-12 physical and mental summaries, return to work, and persistent pain. The primary outcome $Y_t$ is the Glasgow score, and the primary mediator $M_t$ is the SF-12 mental summary. Persistent pain is a secondary mediator in a two-step chain, with pain coming before mental health. Physical recovery $L_t$, the SF-12 physical summary, is the treatment-affected confounder.
The treatment contrast must be one the registry actually records. We would first confirm that procedure coding allows operative versus non-operative management of a common fracture group, ideally distal radius or lower-limb fractures. These are the settings where convergence is documented. If coding is too coarse, the fallback is discharge to inpatient rehabilitation versus discharge home. That contrast has known confounding by indication, so the baseline covariate set must be rich: injury severity, age, comorbidity, socioeconomic disadvantage, compensable-injury status, and pre-injury work.
The estimator works in two parts. Within each wave pair, we estimate interventional direct and indirect effects with cross-fitted, doubly robust estimators in the style of crumble. The past is sequential: baseline, then $L_{6}$, then $M_{6}$, then $L_{12}$, then $M_{12}$, then $Y_{24}$. Loss to follow-up is handled by inverse-probability-of-censoring weights inside the same influence function. That keeps the method robust to misspecification of either the outcome models or the treatment-and-censoring models. Because every wave's estimate is a sample average of an influence function computed on the same patients, the convergence decomposition above is a linear contrast of those functions. A multiplier bootstrap then gives joint confidence regions across waves and a direct interval for the convergence share, $\rho = [\mathrm{IIE}(t_1)-\mathrm{IIE}(t_2)]/[\mathrm{TE}(t_1)-\mathrm{TE}(t_2)]$.
A secondary analysis targets heterogeneity. Following the TEAM secondary analysis (Individualised treatment effects of enhanced early mobilisation in mechanically ventilated patients: a secondary analysis of the TEAM trial), where a null average hid individual mortality effects from −34.0% to +39.3%, we regress the per-patient influence-function values for direct decay and for psychological change on baseline traits. This tests whether average convergence hides opposite-signed subgroups.
We state the limitations plainly. The SF-12 mental summary is a coarse stand-in for constructs such as pain catastrophizing or self-efficacy, which retrospective records rarely contain. Three waves cannot locate the exact time at which curves meet. Sequential ignorability given measured history is an assumption, so we include sensitivity analysis.
Baselines
The naive reference point is the unadjusted difference in mean Glasgow score between arms at 6, 12 and 24 months, the analysis convergence papers usually report. It shows whether convergence exists in the registry at all. If the naive gap does not shrink, the decomposition question does not arise for that contrast.
The conventional comparator is the analysis in the registry paper itself: a multivariable random-effects regression of outcome on treatment, wave and baseline covariates, with mental summary added as a covariate to get a Baron–Kenny-style "explained" share. This is what a clinical reviewer would expect. The relevant prior evidence is simulation-based. In Disentangled Representation for Causal Mediation Analysis, linear structural equation models showed more than 7% bias in the natural direct effect under latent confounding, against 1.5% for that paper's disentangled model and 5.2% for an earlier deep model. Those figures come from a cross-sectional synthetic benchmark and do not carry over directly. For the registry itself, no reported result found on Lacuna for causal mediation estimates. The 24-month descriptive benchmarks (26% full recovery, 71% return to work) characterize the cohort but are not effect estimates to beat.
The strongest competitor, and the key ablation, is wave-by-wave crumble. It runs the same doubly robust interventional mediation estimator separately at each follow-up, with the same covariates, the same learner library and cross-fitting folds, and the same censoring weights. It does not condition on the full sequential history, and it does not form the joint across-wave contrast. Each wave's interval is computed independently, so intervals for differences are approximated by combining them as if the waves were independent. Comparing it with our estimator isolates the two ingredients we add: modeling the physical-recovery-to-mood feedback across waves, and inference on the change in effects rather than on each wave separately.
A further baseline is tvmediation from the time-varying mediation paper, run on the three waves as a coarse varying-coefficient model. It represents the existing dynamic-mediation approach, which has no time-varying confounding adjustment.
All methods receive identical data extracts and the same tuning budget, with learner hyperparameters chosen by the same cross-validation.
Our method beats a baseline if, in semi-synthetic simulations with known truth built on the registry's real covariates, it keeps bias in the convergence share below that baseline's and near-nominal joint coverage, while the baseline does not. On the real data, the comparison is informative if the methods disagree on which hypothesis, ceiling, catch-up or masking, is supported.
Why not just…?
Why not just run Baron–Kenny or a structural equation model at each wave? These methods condition on mental health while also adjusting for physical recovery. Physical recovery is itself caused by treatment, so this conditioning can open a non-causal path between treatment and outcome and bias both direct and indirect estimates. The bias reported in the disentangled-representation simulations points the same way. Our semi-synthetic study measures how much bias this produces on registry-shaped data rather than assuming it.
Why not just apply crumble separately at each wave? This is the real threat. If physical recovery does not feed back into later mood very much, the per-wave estimates will nearly coincide with ours, and only the joint interval for the change adds value. We test this directly. The simulations vary feedback strength from zero upward, and on the real data we report how far the wave-by-wave and sequential estimates diverge. If they agree within error, we will say so and present the decomposition and joint inference as the contribution, not the sequential modeling.
Why not just use the functional doubly robust estimator of the effect curve? That estimator yields total effects only, so it cannot separate direct decay from psychological change. With three follow-up waves, smoothing a curve adds assumptions rather than information. We borrow its emphasis on joint inference across time, implemented through the bootstrap over waves.
Why not just run a randomized trial? Trials such as TEAM can randomize treatment, but they cannot randomize mood. The mediation question stays observational even inside a trial. Trials also exclude the litigating, disadvantaged, and multiply injured patients that a population registry covers.
Proposed Experiments
The first experiment is a semi-synthetic simulation. It keeps the registry's real baseline covariates and attrition pattern and generates treatment, physical recovery, mental health and outcome under each of the three hypotheses, at several strengths of physical-to-mood feedback. The decisive measure is bias and joint coverage for the convergence share. Our estimator should stay near nominal in every scenario, while the regression baseline, and the wave-by-wave baseline under strong feedback, should either favor the wrong hypothesis or under-cover.
The second experiment is an external positive control on the Wisconsin Smokers' Health Study 2 data. There, negative-affect mediation was strongest in week one and faded faster for the nicotine patch than for varenicline or combination therapy. Applying our decomposition to weekly aggregates should recover that faster decay in the patch-versus-intensive contrast.
The third experiment is a divergence check on the SHARE cohort, where the functional doubly robust estimator found quality-of-life gaps widening with age. Our estimator, restricted to total effects, should reproduce that sign pattern and should not manufacture convergence.
The main analysis then estimates the convergence share for the chosen registry contrast. A tipping-point sensitivity analysis reports how strong an unmeasured confounder of mood and outcome would need to be to move the share across zero.
The result that matters most is a convergence share whose interval excludes zero in either direction. In particular, a persistent direct effect cancelled by an opposite indirect effect would mean that "equal outcomes at two years" is not, by itself, evidence that two treatments are interchangeable.
References
- Evaluation of the effectiveness of ankle arthrodesis options
- Distal radius fracture: review
- Pulmonary Rehabilitation Accelerates the Recovery of Pulmonary Function in Patients With COVID-19
- All-Arthroscopic versus Mini-Open Repair of Small to Large Sized Rotator Cuff Tears: A Meta-Analysis of Clinical Outcomes
- Efficacy and safety of three-dimensional printing technology assisted open reduction and internal fixation versus conventional surgery in the treatment of acetabular fractures: a meta-analysis of randomized controlled trials
- PREDICTORS OF LONG TERM OUTCOMES FOLLOWING MAJOR TRAUMA: A POPULATION-BASED STUDY
- Exploring the relationship between social exclusion and smartphone addiction: The mediating roles of loneliness and self-control
- Sleep Reactivity and Depressive Symptoms Among Chinese Female Student Nurses: A Longitudinal Mediation Analysis
- The relationship between uncertainty and acute procedure anxiety among surgical patients in Chinese mainland: the mediating role of resilience
- General targeted machine learning for modern causal mediation analysis
- Doubly-Robust Functional Average Treatment Effect Estimation
- Estimation and Inference for the Mediation Effect in a Time-varying Mediation Model
- Individualised treatment effects of enhanced early mobilisation in mechanically ventilated patients: a secondary analysis of the TEAM trial
- Disentangled Representation for Causal Mediation Analysis