When people report pain, soreness, or fatigue, their answers mix two things: what their tissue is actually doing and how they happen to be reporting it. How they report depends on expectations, current mood, and what they think the investigator wants to hear. Studies that link symptoms to biology almost never separate these two parts. Every "objective" marker they use is either validated against the same self-reports or is itself effort-dependent. We propose a controlled experiment that separates them. It uses a tissue measurement from diffusion MRI, which tracks how far water molecules wander in tissue. The key feature is that the measurement is repeated at several "diffusion times," meaning how long the water is allowed to wander. At short diffusion times water moves freely. At long ones it keeps bumping into cell membranes. How much the apparent motion shrinks as diffusion time grows is therefore a readout of membrane barriers, and it cannot be influenced by what the participant believes.
The design has two factors. The first is tissue damage, and it is within each person: one shoulder muscle is damaged by eccentric exercise and the other serves as the control. The second is expectation, and it is randomized between people: participants are told either that a recovery aid will speed their recovery or nothing. If the diffusion readout tracks the damaged side but does not respond to the expectation framing, while symptom reports respond to both, then the gap between reports and tissue gives a person-level, quantitative estimate of expectation bias. That gap can then be decomposed into its momentary and recall components. As far as we can tell, no one has turned a physical tissue measurement into a calibrated instrument for measuring reporting bias itself.
Core Claim
A differential diffusion metric can serve as a symptom anchor whose measurement error is independent of how people report. The metric is the change in mean diffusivity or anisotropy between a short and a long diffusion time, measured within one acquisition. Such an anchor makes the expectation-driven and recall-driven parts of symptom reports identifiable in a way that neither self-report comparisons nor effort-dependent physical tests allow.
The claim is specific. We are not saying diffusion MRI can "validate" a subjective state. Soreness is subjective by definition. What diffusion MRI can do is supply one tissue quantity. Under a randomized expectation manipulation, that quantity should stay put while reports move. Because it stays put, the movement in reports can be attributed to the reporting process rather than to the tissue.
Why this intersection, and what the prior work does and does not do
The self-report literature gathered here motivates the problem but leaves it unsolved. NeCamp et al.'s micro-randomized trial in 1,565 medical interns found that the same mood-boosting notification raised self-reported mood by 0.19 points in interns whose prior mood score was 3, but lowered it by 0.12 points in those whose prior score was 9. This shows that reports react to interventions in ways that depend on the person's prior state. With no tissue measure, however, the authors could not say whether mood or reporting changed.
Other work runs into the same wall. RECOVER-Adult's ME/CFS analysis flags reliance on retrospective recall of fluctuating symptoms such as post-exertional malaise. Cheng et al. relate cortical thickness in children to pain classified by parental questionnaire and acknowledge that this label may be subjective.
Two existing strategies are close to our goal but do not remove the problem. Tag2Risk replaces surveys with passive music-listening traces, yet trains against the self-reported K10 distress scale, so its 66.4% accuracy inherits the bias it set out to avoid. The connectome-imputation study recovers statistical power from missing phenotypes by treating them as missing at random. That approach reproduces any systematic reporting bias rather than estimating it. All of these papers are motivation: they document the gap and constrain what counts as an answer.
The imaging side supplies the method. Marth et al. acquired stimulated-echo (STEAM) diffusion tensor imaging of the supraspinatus muscle at diffusion times of 100, 200, 400 and 600 ms. STEAM is a pulse sequence that stores the signal during a mixing period so that long diffusion times cost little extra signal decay. Across that range, fractional anisotropy (FA, how directional the water motion is) rose and mean diffusivity (MD) fell. Test–retest reliability was excellent for FA (intraclass correlation, or ICC, at least 0.911) and good for MD (ICC at least 0.759). This is our acquisition and our reliability reference.
Chowdhury et al. supply the analysis idea. They showed in simulation and in cell pellets that subtracting diffusivity at two diffusion times (20 ms and 100 ms) cancels static confounds, namely cell radius and volume fraction, and isolates membrane water exchange. Exercise-induced muscle damage is, at the cellular level, largely a membrane-integrity injury. The differential metric therefore targets the biology we care about rather than generic edema.
Two papers constrain the design. Feng et al. show that changing echo time shifts compartment-weighted diffusion parameters, with coefficients of variation up to about 34% for pseudo-diffusion. Any design that lengthens diffusion time by lengthening echo time would therefore mix tissue relaxation effects into the time-dependence. STEAM keeps echo time fixed and varies the mixing time instead. We additionally acquire a non-diffusion-weighted image at every mixing time, so that longitudinal relaxation during mixing divides out of each diffusivity estimate. Grussu et al. found that in clinical spinal-cord data, richer compartment models improved fits in most voxels but significantly in few, because noise was high. We therefore use model-free differential metrics rather than fitted cell radii. Bailey et al. show that a single apparent diffusion coefficient is a composite, correlating with both intracellular diffusion (r = 0.48) and perfusion fraction (r = 0.46). This is why a single-time metric is the baseline to beat rather than the anchor.
Research Program
We recruit healthy adults who undergo unilateral eccentric shoulder-abduction exercise that loads one supraspinatus; the other shoulder serves as the control. Participants are then randomized to one of two framings. In the expectation framing, they receive an inert "recovery aid" described as accelerating repair. In the neutral framing, they receive only standard instructions. Scanning happens at baseline and at roughly 24, 48 and 96 hours after exercise, following the Marth protocol: STEAM at four diffusion times plus a spin-echo acquisition at about 19 ms. We add quantitative T2 mapping, because T2 (the signal-decay time that lengthens with tissue water) is the conventional muscle-edema marker.
Symptom reports come at two timescales. Momentary soreness for each shoulder is collected by smartphone prompts several times a day, following the ecological momentary assessment logic in NeCamp et al. On day 7, participants give a retrospective report of peak and average soreness for each shoulder, along with a current-mood item.
The primary tissue quantity for each shoulder $s$ at each visit is the differential diffusivity
$$\Delta D_s = \mathrm{MD}_s(100\,\mathrm{ms}) - \mathrm{MD}_s(600\,\mathrm{ms}),$$
and its FA analogue. Each is expressed as the change from that shoulder's own baseline. Intact sarcolemmal membranes should produce a large drop in diffusivity between 100 and 600 ms. Leaky, damaged membranes should shrink that drop, which is the same logic Chowdhury et al. use for aquaporin-driven exchange.
Momentary reports are then modeled as
$$R_{ist} = \lambda\, \Delta D_{is} + \beta_F F_i + \gamma\, M_{it} + u_i + \varepsilon_{ist}.$$
Here $R_{ist}$ is person $i$'s soreness report for shoulder $s$ at time $t$. $\Delta D_{is}$ is the interpolated tissue anchor. $F_i$ is the randomized framing indicator. $M_{it}$ is concurrent mood. $u_i$ is a person-level reporting offset, and $\varepsilon_{ist}$ is residual noise. The coefficient $\beta_F$ is the expectation bias, the shift in report per unit of tissue change that is caused by framing. $\gamma$ captures mood-congruent reporting.
Recall bias is estimated separately. It is the gap between the day-7 retrospective report and a tissue-weighted summary of the momentary reports, tested for dependence on framing and on day-7 mood.
Identification rests on one assumption, which we test rather than assume: the anchor's measurement error is independent of framing. The same model also yields each participant's estimated $u_i$. That is the product that could later be carried into clinical cohorts as a reporting-style covariate.
Baselines
The naive reference point is self-report alone. It is the difference between the exercised and control shoulders in momentary soreness, compared across framing arms, with no tissue anchor. This design can detect that framing shifts reports. It cannot say whether framing shifted the reports or the healing. If framing produced a real placebo-type reduction in tissue damage, the report-only analysis would misread genuine improvement as bias. The proposal beats this baseline if the anchored model assigns a framing effect that differs materially from the raw report difference, or if it assigns the same effect with the tissue explanation ruled out.
The strongest existing tissue marker is quantitative T2 and single-diffusion-time spin-echo diffusion, run in the same sessions on the same participants and regions of interest. We use identical outlier and motion rules for all three, and we pre-register a single summary metric per method (change from baseline, averaged over the muscle) so that no method gets extra tuning. For spin-echo diffusion, Marth et al. report FA ICC = 0.960, MD ICC = 0.752 and SNR of 72.3, against STEAM FA ICC of at least 0.911 and SNR of 29.2 to 40.1. The spin-echo baseline therefore starts with a signal-to-noise advantage. For the sensitivity of T2 or diffusion to exercise-induced supraspinatus damage, we found no reported result on Lacuna.
Beating these baselines means two things. The differential metric must show at least comparable test–retest reliability on the control shoulder. It must also show a larger ratio of damaged-versus-control effect to between-session noise. Equally important, it must explain report variance that T2 does not, measured as a gain in explained within-person variance when $\Delta D$ is added to a T2-only model.
The key ablation removes the time-dependence while keeping everything else fixed. We replace $\Delta D$ with STEAM mean diffusivity at a single diffusion time, either 100 ms or 600 ms alone, from the same acquisition. If a single long-diffusion-time value performs as well as the difference, the gain comes from STEAM contrast rather than from probing restriction across diffusion times. The differential idea would then be unsupported.
The final behavioral comparator is maximal voluntary contraction strength loss, the standard physical muscle-damage marker. It is measured at every visit.
Why not just…?
Why not just compare momentary reports to retrospective recall, with no imaging? For pure recall bias this works, and we use it. It answers only half the question, however. It assumes momentary reports are truthful, and NeCamp et al.'s state-dependent shifts in daily mood reports show that momentary reports themselves respond to interventions. Expectation bias acts at the moment of reporting, so a within-report comparison cannot see it. The report-only baseline above makes this concrete. If the anchored and unanchored estimates of the framing effect coincide and the anchor adds nothing, this alternative wins, and we will say so.
Why not just use strength loss or a blood marker as the objective anchor? Strength loss is the real threat, because it is cheap, side-specific and standard. But maximal voluntary contraction depends on effort, and effort is exactly what expectation framing may change. We test this directly: if framing shifts strength loss, strength cannot anchor bias estimates. If framing does not shift it, and strength tracks side-specific damage as well as $\Delta D$ does, then imaging is unnecessary for this question and the proposal should shift toward strength-anchored field studies. A circulating marker would reflect both shoulders together and so cannot use the within-person contrast.
Why not just use T2 mapping or standard diffusion tensor imaging? Both are faster and have better signal-to-noise. Edema, however, is a mixed signal of fluid shifts and inflammation, and single-time diffusivity is a composite of several tissue properties, as Bailey et al. show for the apparent diffusion coefficient. The differential metric is designed to cancel static structure and to target membrane restriction, following Chowdhury et al. Whether that specificity matters in vivo at 3 T is an open empirical question given Grussu et al.'s noise findings. The ablation and the incremental-variance test settle it. If T2 alone carries the anchor, we adopt T2.
Decisive Experiments
The first check is discriminant validity of the anchor. The damaged-versus-control difference in $\Delta D$ should be clearly nonzero at 24 to 48 hours. The interaction between framing and side should fall within a pre-registered equivalence margin. Reports should show both the side effect and a framing effect. An anchor that moves with framing is disqualified, whatever its correlation with reports.
The second check is reliability. Using two baseline sessions and the control shoulder throughout, we compute ICCs for $\Delta D$ and compare them to Marth's single-time STEAM values. A difference of two noisy quantities can be less reliable than either one, which is the main technical risk. If the ICC for $\Delta D$ falls well below the single-time MD ICC, we fall back on fitting the full diffusion-time curve across all four time points rather than using a two-point difference.
The third check is the bias decomposition itself. We estimate $\beta_F$ with the anchor, without it, and with T2 or strength in its place. We then test whether day-7 recall departs from tissue-weighted momentary reports in proportion to day-7 mood. That would be mood-congruent recall, the mechanism RECOVER-Adult worries about in post-exertional malaise.
A positive result on all three checks yields a calibrated, person-level reporting offset. The natural next step is to carry that offset into patient cohorts in which exertional symptoms are currently known only through recall.
References
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- Incidence and Prevalence of Post-COVID-19 Myalgic Encephalomyelitis: A Report from the Observational RECOVER-Adult Study
- Abnormal structural gray matter and structural covariance networks associated with biopsychosocial characteristics in children with multisite pain
- Tag2Risk: Harnessing Social Music Tags for Characterizing Depression Risk
- Rescuing missing data in connectome-based predictive modeling
- Stimulated echo acquisition mode (STEAM) diffusion tensor imaging with different diffusion encoding times in the supraspinatus muscle: Test–retest reliability and comparison to spin echo diffusion tensor imaging
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