Does the Body Lock In the Stroke Plateau? A Self-Remodeling Neuromechanical Model of Post-Stroke Arm Recovery

After a stroke, most arm recovery happens in the first few months. After that, improvement nearly stops. A meta-analysis of control groups found chronic patients on usual care gain only 0.9 ± 1.66 points on a 66-point arm impairment scale (Upper limb motor recovery in chronic stroke). The usual explanation is that a brain "plasticity window" closes. A second explanation gets less attention. The body itself changes after weeks of reduced and distorted use: muscles shorten and stiffen, reflexes heighten, and the patient learns to lean the trunk instead of reaching. These changes may make the compensatory way of moving the cheapest one available, so that the recovering nervous system settles into it. This is the stroke version of the acute-to-chronic modeling gap (The Acute to Chronic Disease Modeling Gap). Treatments are designed against the acute injury, but chronic disability is governed by slow secondary remodeling.

We propose to test this second explanation in simulation. We will build an embodied neuromechanical model: a simulated arm and trunk with muscles and physics, driven by a lesioned, learning neural controller. In ordinary models of this kind the muscle and tendon parameters are fixed. In ours they slowly remodel according to how the simulated patient uses the arm. We then ask two questions. Does a time-limited therapeutic window, and a later plateau, emerge from the coupling of motor learning and tissue remodeling, without any hard-coded expiry of brain plasticity? And does the model correctly predict which therapies break the plateau and what compensation patterns appear, where simpler models cannot?

Core Claim

Embodied simulations currently assume a static body (The embodied brain: neuromechanical digital twins). The closest stroke-specific attempt couples a virtual mouse spinal cord and musculoskeletal model to cortical recordings, but keeps its stroke network models in a separate pipeline and its body fixed (Allegra Mascaro et al.). Our central claim is falsifiable. If use-dependent muscle remodeling is added to a closed-loop model with a lesioned learning controller, then two things follow. First, the model produces a delay-dependent loss of rehabilitation benefit, so that the same training dose helps less when started late. Second, it produces a chronic plateau. The same model with a static body should produce neither. Removing plasticity decay from the brain side should leave both intact. If the static-body ablation also produces a window, the claim is wrong, and we will report it as such.

Research Program

The body is an upper-limb-plus-trunk musculoskeletal model in OpenSim or MuJoCo. It has Hill-type muscles, which are standard muscle models where force depends on activation, fiber length, and velocity. The trunk is included because trunk synergies are recruited in almost every arm task and are disrupted after stroke (Muscle synergy analysis yields an efficient and physiologically relevant method). A wrist-only model would hide exactly the compensation we care about (Automated Movement Assessment in Stroke Rehabilitation).

The controller has three layers. The cortical layer has a fraction of its descending output channels removed to represent the lesion. The spinal layer consists of motor pools with stretch reflexes whose gain can rise. The top layer is a learning policy trained by reinforcement with an effort cost. We do not need spiking cortex for this question. The spinal and muscle stages follow the result that decoded motor neuron drive can predict joint torque through a forward musculoskeletal model (In Vivo Neuromechanics).

The new ingredient is a slow tissue loop. Each muscle has a maximum force $F_i$ and an optimal fiber length $\ell_i$, and both drift toward targets set by recent use:

$$\tau_F \dot F_i = g(\bar a_i) - F_i,\qquad \tau_\ell \dot\ell_i = h(\bar\ell^{\text{op}}_i) - \ell_i,$$

Here $\bar a_i$ is the muscle's time-averaged activation and $\bar\ell^{\text{op}}_i$ its time-averaged operating length over simulated days. The function $g$ captures disuse atrophy and $h$ captures sarcomere loss when a muscle is held short, which produces contracture. The time constants $\tau_F$ and $\tau_\ell$ are set on the order of weeks.

Simulated "days" alternate between two kinds of episodes. Free-living episodes let the policy choose its own movement strategy for daily reaching tasks. Prescribed therapy episodes vary in dose, start time, and assistance mode. One mode is triggered only when the user exceeds 20% of maximum voluntary torque, following Susanto et al.. The other is passive. A simulated impairment score is computed by rule from model performance on a subset of Fugl-Meyer upper-extremity items that can be reproduced in the simulation, alongside muscle synergies extracted by nonnegative matrix factorization from simulated muscle activity.

Calibration uses only healthy kinematics and acute-phase severity distributions. Every chronic and therapy-response target is held out. We are explicit about scope: this is a mechanism test against published signatures, not a patient-level forecaster. No public longitudinal joint-level dataset spanning acute to chronic stages appears in the file.

Baselines

The naive reference point is a no-remodeling, no-learning model: the lesion is applied, nothing adapts, and the impairment stays at its acute value forever. It sets the floor and checks that our simulated scoring captures lesion severity at all.

The strongest existing mechanistic competitor is a static-body closed-loop neuromechanical model in the style of Allegra Mascaro et al.. That work reports 13% mean absolute error on mouse slide displacement. We run it as the identical model, with the same body, controller, learning rule, compute, and number of simulated days, but with $\tau_F,\tau_\ell \to \infty$. This is also the ablation that isolates our key ingredient. We beat it if our model reproduces three held-out effects and the static model reproduces at most one: a start-delay penalty on rehabilitation, a usual-care plateau with gains below the minimal clinically important difference, and a benefit of triggered over passive assistance.

A second ablation swaps mechanisms. We give the static-body model an explicit, decaying brain-plasticity rate. This tests whether a hard-coded neural window explains the same data equally well. If it does, the two mechanisms must be separated by the joint-level signatures described in the experiments below.

The strongest statistical competitor for outcome prediction is Elastic-Net regression on baseline impairment and the difference in motor threshold between hemispheres. It reports $R^2 = 0.910$ for post-therapy Fugl-Meyer in 102 chronic patients (Predicting response to motor therapy in chronic stroke). We do not expect to beat it at point prediction and will not claim to. The comparison is on counterfactual timing questions, where we found no reported result on Lacuna for any model predicting the effect of rehabilitation start time on chronic outcome.

Why not just…?

Why not just fit a statistical recovery model? For predicting a chronic score from baseline, the Elastic-Net result above is already excellent. The same work found that adding structural MRI disconnection did not help, which warns against assuming richer inputs win. But such a model is fit on patients whose therapy timing was not varied by design, so it cannot answer "what if training had started at week two instead of month six." Our claim concerns that counterfactual and the mechanism behind it, not prediction accuracy.

Why not just use a two-variable "use it or lose it" dynamical model of arm use and function, with no body? This is the real threat. A low-dimensional model can produce a window and a plateau with a few parameters. We will fit one to exactly the same summary targets. The embodied model earns its cost only if it also predicts joint-level signatures the low-dimensional model has no variables for. The first is that synergy merging increases with severity, while mild cases mostly preserve their synergies, as reported in Evidence of synergy coordination patterns. The second is trunk compensation coexisting with successful wrist trajectories. The third is that triggered assistance outperforms passive assistance at equal dose. If the low-dimensional model matches all three, we will concede that the body is unnecessary for this question.

Why not just refit musculoskeletal parameters at each clinical visit? This descriptive approach, as in Li, Xie et al., revealed an 892% tibialis anterior tension increase in one recovering patient. It tells us what changed, but it cannot generate the trajectory under a therapy that was never given. We use it as a sanity check: our simulated force trajectories should rise in recovering simulated patients in the same direction.

Proposed Experiments

The first experiment is a timing sweep. We start an identical dose of triggered-assistance therapy at simulated weeks 1, 4, 12, and 26 across a population of lesion severities, and measure chronic simulated Fugl-Meyer upper-extremity scores in both the full and static-body models.

The second experiment checks the plateau. Usual-care simulations past three months should show a standardized gain near the meta-analytic 0.11, with confidence interval −0.05 to 0.26. They should also show a positive association between dose and effect, against the reported $r = 0.46$ between rehabilitation hours and effect size (Upper limb motor recovery in chronic stroke).

The third experiment compares therapy modes at chronic onset. Triggered assistance should beat passive assistance, matching the direction of Susanto et al., whose robot group all exceeded the action-arm-test clinically important difference immediately after training. The model should also predict which part of the gain is reversal of contracture and which is policy change, a split no trial can measure directly.

The fourth experiment compares synergy and compensation signatures against the 41-muscle and 10-muscle cohorts, and against the subacute finding that bilateral training helps (Tang et al.).

The decisive check is the cross of remodeling with plasticity decay. We run four conditions: remodeling on or off, crossed with plasticity decay on or off. The proposal stands only if the delay penalty and plateau track the remodeling factor. It also requires that, in late-start simulations, first restoring tissue parameters in silico (a simulated contracture release) brings back most of the early-start benefit. That is the model's own version of the prophylaxis paradox, and it is a prediction a trial could later test.