Naming the nocebo out loud: an eight-week protocol for functional motor symptoms

Functional motor symptoms are the place where expectancy stops being a rounding error and becomes the deficit itself. A New Zealand group built a treatment on precisely that claim, gave it a name that says so, and then did the harder thing: ran it against an active control that received a rival explanation and the same amount of physical work. The registered primary outcome came back empty.

How the eight weeks actually run

Thirty-nine adults were referred from public neurology services in Dunedin after a neurologist had made the diagnosis. Randomisation used sealed, opaque, sequentially numbered envelopes and blocks of 20. Both arms opened with a session of roughly 90 minutes, always delivered by a clinical psychologist; everything afterwards was movement work run by a physiotherapist together with a psychologist or other allied health staff. Individual staff delivered only one of the two treatments, to limit contamination. Total therapy was capped at 25 hours over eight weeks, with sessions of 30 to 120 minutes. Actual dose was comparable: median 9.13 hours (IQR 5.25 to 15.25) in the protocol arm against 12.00 hours (IQR 7.00 to 25.00) in the control arm, P = 0.236.

Session one of Nocebo Hypothesis CBT is an explanation and nothing else. The clinician introduces the nocebo effect as a concept, then hands the patient a personalised formulation of how an implicit belief of being neurologically damaged is producing their weakness, tremor or gait failure. In the sessions that follow the clinician films the patient attempting a relevant physical task, then introduces a distractor agreed with the patient beforehand and made as engrossing as possible: their own music, irrelevant conversation. Movement usually improves under distraction. That improvement is filmed and replayed to the patient immediately, and the clinician states what the recording means out loud: structural damage does not switch itself off when you change the subject. Tasks escalate across sessions until the symptom no longer appears; the ceiling stated anywhere in the trial is walking on a treadmill at 5.0 km/h.

The control arm is what makes the trial worth reading. Those patients also received a 90-minute first session, also received a causal explanation, that their symptoms reflect a "misprogramming" in the brain, also received supportive counselling and staged movement retraining. What the manual forbade them was visual feedback of any kind, no mirrors and no video, engrossing distraction, only fixation on a point in space, and any explicit statement that full recovery was expected. So the comparison is not therapy against nothing. It is one causal story plus filmed counterevidence against another causal story without it.

What the numbers will and will not carry

The primary endpoint was pre-registered on the Australian New Zealand Clinical Trials Registry as SF-36 Physical Functioning with an eight-week primary timepoint, and that is exactly what the paper reports. Between groups: d = 0.21, 95% CI -0.42 to 0.84. Both arms improved markedly from baseline, which is what an unblinded, intensive inpatient programme delivering two credible rationales should produce, and it is precisely why the large within-group changes cannot be read as the protocol working. Global impression of improvement, which the registry lists as self-rated, was indistinguishable between arms at eight weeks, 1.58 against 1.61, P = 0.900.

Three secondaries carried intervals above zero at eight weeks, and mobility on the Functional Mobility Scale still did at 16 weeks. That is a signal. It is not a verdict, for reasons the authors state themselves: the trial enrolled 39 of a planned 172 participants, attempts to add Australian and New Zealand sites failed, and the study was reconceived mid-course as a phase IIb pilot with the pre-planned mixed-model analysis replaced by effect-size estimation. Twenty-two outcome measures were read without correction for multiple comparisons.

The 85% against 47% recovery figure deserves separate handling, and the reason is not the one you would guess. Recovery was defined as the participant considering themselves free of functional motor symptoms, plus walking at 5.0 km/h for 15 seconds, plus a minimum of therapy delivered, and the 2020 protocol paper introduced that combination as the criterion for ending treatment early. The paper reports it openly under clinical significance, so there is no concealment here. But it means the measure was judged by the unblinded therapists delivering the treatment, partly on the patient's own say-so, while the blinded assessor rated mobility only. Now put that next to the manuals. The experimental manual instructs therapists to use purposeful optimism and to convey as much optimism as possible about potential recovery; the control manual states that purposeful optimism should not be part of the therapist's approach. A difference in how confidently recovery was predicted to the patient loads directly onto the one outcome that is subjective, unblinded and doubles as the stop rule. That is why this contrast cannot be read as a treatment effect, and it is a sharper objection than the outcome merely being absent from the registry, which it also is: it does not appear among the 18 secondary outcomes registered on ANZCTR. The registry record itself is prospective and clean on every point that matters: submitted 3 April 2020, registered 11 May 2020, first participant enrolled 19 June 2020, with the same primary outcome and the same instrument list. It has simply not been updated since 10 October 2022, so it still reads "Recruiting" with an accrual of 38.

For your practice

What transfers is not the programme, it is the sequence. Nocebo Hypothesis CBT is structurally a behavioural experiment, so calling it new would be overstating it, but the target is unusually narrow: one implicit belief about neurological damage, with emotion regulation, symptom triggers and trauma explicitly left alone. The manuals differ on five points, and the one that matters most is that this protocol states an expectation of full recovery out loud while the control protocol forbids it. The data match that narrowness. Anxiety and depression showed between-group effects near zero, and the authors say plainly that emotions were never a therapeutic target. If you work with functional motor symptoms, the usable element is explaining the mechanism as expectation rather than damage and then generating a filmed counterexample in the same hour, so the patient sees the disconfirmation rather than being told about it.

Two things bound that. The trial ran on an inpatient neurorehabilitation ward with a physiotherapist in the room; an outpatient clinician has neither the equipment nor the daily contact, and the trial says nothing about whether the protocol survives that translation. Fidelity ratings also suggested that some control patients received elements of the experimental protocol, and two control participants, among the most disabled in that arm, were switched to it before the eight-week assessment. Both would narrow the gap rather than widen it, but neither is a reason to treat the secondary outcomes as confirmed.

Safety looked unremarkable and was measured rather than assumed: 10 adverse events in total, all classified as minor or minimal, none serious, with no difference between arms, P = 0.571. Therapeutic alliance scores did not differ. So the honest position to hold on Monday is this. The explanation is worth borrowing, because it is coherent, it is respectful of the patient, and it does not require the clinician to imply the symptom is imaginary. The efficacy claim is not yours to make yet, and the authors are not making it either; they asked for a definitive trial.