Is the Injured Brain's Anatomy Doing the Diagnosing? Auditing Atlas-Based fMRI Markers of Covert Consciousness

Some patients who appear completely unresponsive after severe brain injury are in fact aware. They cannot show it because the damage has cut the pathways that drive movement, a condition called cognitive motor dissociation (CMD). Because bedside diagnosis depends on watching for movements, these patients are missed. A promising alternative is to classify patients from resting-state functional MRI (rs-fMRI), brain activity recorded while the patient simply lies in the scanner, so that no command-following is needed. The best such result trains a support vector machine on how stable functional connectivity between brain networks stays over time. It separates patients from healthy controls with an AUC of 0.85 at an independent center and correctly flags all four CMD patients in a small test cohort (Identifying patients with cognitive motor dissociation using resting-state temporal stability).

These features depend on a step that is easy to overlook. Each brain is first warped onto a standard healthy template, a step called spatial normalization, so that "default mode network" refers to the same voxels in every subject. Injured brains contain contusions, enlarged ventricles, and missing bone, and they move more in the scanner. Warping such a brain onto a healthy template can drag healthy tissue into lesion cavities and mix cerebrospinal fluid into network regions. Any of these could make connectivity look "unstable" whether or not the patient is conscious. We propose to measure how much of the reported diagnostic signal comes from this anatomy and motion. We also propose a pipeline that removes it: features are computed in each patient's own anatomical space, every network region is weighted by how well it registered, and the reliability information is stored in a shared, standardized data format so that small cohorts from many centers can be pooled.

Core Claim

Our hypothesis is falsifiable. A large share of the separability between disorders-of-consciousness patients and controls in atlas-normalized rs-fMRI features can be predicted from nuisance variables alone: lesion and ventricle volume, registration quality, and head motion. A classifier built on registration-reliability-weighted, native-space features will keep its accuracy on the clinically relevant contrasts, which are minimally conscious versus unresponsive patients and CMD versus non-CMD patients under leave-one-site-out testing, while the standard pipeline will lose accuracy there. If the nuisance-only model cannot approach the published performance, that is also a useful result. It would be the first direct evidence that the temporal-stability marker is not an artifact of injury anatomy.

The idea differs from the closest work in what it treats as the object of study. Identifying patients with cognitive motor dissociation using resting-state temporal stability motivates the proposal. It uses standard atlas normalization without testing whether lesions distort it, and its CMD test rests on 11 patients scanned a mean of 116 days before the BCI assessment that labelled them. Distributed harmonic patterns of structure-function dependence orchestrate human consciousness decomposes patient fMRI onto the wiring modes of a healthy-template connectome and finds that unconsciousness is tied to activity collapsing onto low-frequency structural modes. Our audit applies directly there: a damaged brain projected onto healthy wiring might look "structurally slaved" for geometric reasons. We do not reject either finding. We test whether each one survives once the anatomical confound is controlled.

Research Program

The method for the audit comes from A survey of patient motion in disorders of consciousness and optimization of its retrospective correction. That study injected real patient motion traces into clean scans and measured how much activation correction could recover, finding a ceiling near 80%. We extend the injection idea from motion to anatomy. We take lesion masks, ventricular enlargement, and craniectomy geometry from patient structural scans and transplant them into healthy control data. In practice, the patient's deformation field and tissue loss are applied to a control's structural and functional images, with signal in the lesion zeroed or replaced by fluid-like signal. We then run the unchanged standard pipeline. The quantity of interest is the spurious shift

$$\rho_k = \frac{f_k(\text{control with injected injury}) - f_k(\text{control})}{f_k(\text{patients}) - f_k(\text{controls})},$$

where $f_k$ is the mean of temporal-stability feature $k$, such as default-mode-network stability, in the indicated group. A value of $\rho_k$ near 1 means the injected anatomy alone reproduces the patient–control difference for that feature. A value near 0 means the feature is robust. The same injection can be combined with real patient motion profiles to separate the anatomical and motion contributions.

The corrected pipeline has two parts. First, each atlas region is pulled back into the patient's own space through the inverse warp, and connectivity is computed there. Second, each region receives a reliability score from its overlap with lesioned tissue, the local deformation magnitude, and the local temporal signal-to-noise. Low-reliability regions are down-weighted or treated as missing rather than silently filled in. This matches the observation in Few-shot image segmentation for cross-institution male pelvic organs using registration-assisted prototypical learning, where removing explicit alignment cost at least 12% in cross-institution tests, so alignment quality matters for small-sample transfer. Unlike that work, we do not learn the alignment. With tens of patients, a learned alignment module would be one more thing to overfit.

Standardized data organization is the enabling constraint, not the contribution in itself. Following The brain imaging data structure, a format for organizing and describing outputs of neuroimaging experiments, BIDS is a folder-and-filename convention with machine-readable metadata files. Following Clinica, standardized derivative folders can carry processed outputs. We will define a disorders-of-consciousness derivative containing four things: lesion masks, per-region reliability scores, behavioral subscores from the Coma Recovery Scale-Revised, and BCI outcomes, each timestamped. The timestamps let every analysis be restricted to assessments within a fixed window of the scan, which directly addresses the 116-day gap. Clinica's pipelines were built for neurodegeneration and have no lesion handling. Our derivative adds exactly the fields needed to pool injured-brain cohorts across centers.

Modeling stays deliberately simple. Scaling behaviours of deep learning and linear algorithms for the prediction of stroke severity acts as a constraint. On spatially normalized lesion data, regularized linear models beat an 8-layer network at n = 100 ($R^2$ 0.279 vs 0.250), and deep models only pulled ahead around n = 900. Every disorders-of-consciousness cohort here is far below that. All classifiers will therefore be linear or linear-kernel SVMs with nested cross-validation and a fixed, preregistered tuning grid.

Baselines

The naive reference point has two parts. The first is the majority-class rate on each contrast. The second, more important, is a nuisance-only logistic regression whose inputs are lesion volume, ventricle volume, mean registration error, and mean framewise motion. This is the audit's key comparator. If it reaches an AUC close to the published value on patients versus controls, then much of what is being "diagnosed" is injury and motion rather than consciousness.

The strongest existing method is the temporal-stability SVM of Identifying patients with cognitive motor dissociation using resting-state temporal stability. It reports 90% accuracy and AUC 0.94 on its training center, 82% accuracy and AUC 0.85 on its independent validation center, and 91% accuracy and AUC 0.86 on the 11-patient CMD cohort. We will reimplement it using its stated network set (default mode, frontoparietal, cingulo-opercular, and salience networks) and sliding-window procedure. It will run on the same BIDS-organized cohorts, with the same splits and the same tuning grid as our pipeline. The original cohorts are not public, so we will request them from the authors. Failing that, we will compare on our partner-center data, and the published numbers will serve only as context, not as a head-to-head result. For connectome-harmonic classification there is no reported classification result on Lacuna for Distributed harmonic patterns of structure-function dependence orchestrate human consciousness. We will compute its harmonic-energy features on the healthy template and on patient-specific connectomes and include both as baselines.

Two ablations isolate the key ingredient. The first computes features in native space without reliability weighting. The second applies reliability weighting to standard template-space features. Beating the strongest baseline has a specific meaning. On leave-one-site-out minimally conscious versus unresponsive classification, and on CMD versus non-CMD classification restricted to scans within 14 days of the BCI assessment, the proposed pipeline must show a higher AUC with a bootstrap confidence interval for the difference that excludes zero. It must also show $\rho_k$ substantially below that of the standard pipeline on the injection test. Equal performance on patients versus controls alone would not count as a win.

Why not just…?

Why not just regress lesion volume and motion out of the features? This is the most serious competitor. If one confound-regression step removes the artifact, the native-space pipeline is unnecessary. Global covariates cannot capture region-specific distortion. A frontal contusion corrupts frontoparietal regions and leaves occipital ones intact, so regressing out lesion volume treats all regions alike. The injection experiment settles the question. We will compare $\rho_k$ under covariate regression with $\rho_k$ under the native-space pipeline. If regression reaches comparable $\rho_k$ and comparable within-patient AUC, we will report that and recommend regression as the cheaper fix.

Why not just use bedside EEG and skip MRI altogether? Sensor-space multiscale entropy reached 92.93% test accuracy in Identifying Features of Electroencephalography Associated with Improved Awareness in Persistent Vegetative State via Multiscale Entropy. That figure rests on a 50/50 split of 19 patients, which implies roughly 10 test cases and a very wide confidence interval. A Potential Prognosis Indicator Based on P300 Brain–Computer Interface for Patients with Disorder of Consciousness found that detection accuracy differs sharply by cause of injury. Scalp EEG faces its own anatomical confound: skull defects and lesions change what each electrode sees. Our audit asks the same question for both modalities. EEG is complementary but not a substitute, and extending the reliability audit to source-localized EEG is a natural follow-up.

Why not just pool more data with a larger pretrained model, as atlas-aligned foundation models do? Cross-Subject Modeling for Widefield Calcium Imaging via Atlas-Aligned Spatiotemporal Tokenization shows that fixed anatomical embeddings enable zero-shot transfer across 38 mice. That method relies on intact, head-fixed cortex mapping cleanly onto an atlas, which is exactly the assumption that fails here. A larger model trained on normalized injured brains would learn the registration artifacts more efficiently. At these sample sizes, the stroke scaling results also predict that it would underperform a linear model.

Proposed Experiments

The decisive check comes first and costs the least: the lesion-and-motion injection experiment. It needs only healthy control rs-fMRI and structural scans from patients, and it yields $\rho_k$ for every temporal-stability and harmonic feature under the standard pipeline, covariate regression, and the proposed pipeline. The second experiment fits the nuisance-only classifier and the standard SVM on patients versus controls. A nuisance-only AUC within 0.1 of the standard SVM would itself be a publishable warning for the field.

The third experiment is the clinical test. It covers leave-one-site-out minimally conscious versus unresponsive classification and CMD versus non-CMD classification, using pooled BIDS-organized cohorts. We will add motion-surveyed scans of the kind described by Hoffmann et al. wherever structural data exist. Only scans with a timestamped BCI or behavioral assessment within the preregistered window are used.

We are explicit about power. With single-digit CMD counts, as in the existing cohort of four, no AUC estimate is trustworthy. We will therefore report exact permutation p-values and bootstrap intervals. We treat the CMD contrast as a secondary endpoint until pooling yields at least 20 confirmed CMD patients, and the patients-versus-controls audit and the within-patient level-of-consciousness contrast are the primary endpoints.