Telling Real Muscle Loss from Scanner Change in Serial CT

Cancer patients get CT scans every few months. Automated tools can now measure total muscle and fat volume from each scan, so the rate at which a patient loses muscle could become a routine warning sign of wasting. That rate is computed across visits, though, and between visits hospitals replace scanners, change how images are reconstructed from raw data, and change slice thickness. Each of these alters the images enough to shift what a segmentation network (a model that labels every voxel as muscle, fat, bone, and so on) reports. A patient who seems to lose 4% of muscle volume between two scans may have lost nothing: the second scan may simply have come from a newer machine.

This note proposes to measure that artifact directly and remove it. We would use scan pairs taken so close together that the body cannot have changed, often on the same day, but under different acquisition protocols. From these pairs we estimate, for each pair of protocols, how much apparent change the switch itself produces and how noisy the switch makes the measurement. A per-patient trajectory model then treats the protocol switch as a known source of error. It outputs a drift-corrected rate of muscle and fat change with an honest uncertainty, and it flags a change as real only when it exceeds what the protocol transition could explain.

Core Claim

Longitudinal body-composition velocity is a promising prognostic signal that nobody has yet validated. It cannot be trusted until acquisition-induced change is separated from physiological change, and that separation can be done empirically from physiologically null scan pairs. Our claim has two parts. The first is that raw automated volumetric change across protocol transitions carries a systematic bias and extra variance that are clinically large compared with the changes we want to detect. The second is that a transition-specific error model, fitted on null pairs and carried into per-patient trajectories, will produce velocity estimates that predict survival better and raise fewer false wasting alarms under forward-in-time evaluation than raw velocity, baseline-only indices, or cohort-level covariate adjustment.

Three lines of prior work motivate this. Borys et al. built a volumetric Sarcopenia Index (muscle volume divided by bone volume) with the Body and Organ Analysis pipeline. In 10,340 patients it predicted survival better than BMI and single-slice L3 muscle area (HR 0.56 abdomen, 0.40 thorax). All of their prognostic modeling used a single baseline scan. Their 250-patient longitudinal subcohort served only to show that bone volume stays stable, and they did not examine scanner drift across their 2004–2021 span. Flouris et al. simulated CT acquisitions and showed that intensity-based features are sensitive to dose, reconstruction algorithm, and slice thickness, but they worked on static tumor regions and not on body-composition segmentation. Bordner et al. showed a musculoskeletal MRI model decaying on 5- and 10-year follow-up scans from newer hardware, and they offered no correction. Together these suggest the gap is real. None of them measures it for tissue volumes inside a patient's own trajectory.

Two further works constrain the design. Guo et al. (2022) found that domain generalization and unsupervised adaptation did not beat plain training across a decade of intensive-care data. Guo et al. (2021) found that drift mostly damages calibration and that only feature-level corrections grounded in domain knowledge preserved discrimination. We therefore do not try to make the segmenter invariant. We leave it fixed and correct its outputs with an explicit, measured model of each protocol transition, which is the feature-level, knowledge-grounded route those reviews found under-explored.

Research Program

The measurement model is simple. For patient $i$ scanned at times $t_1$ and $t_2$ under protocols $p_1$ and $p_2$, let $y$ be an automatically extracted quantity such as log muscle volume. We write

$$\Delta y_i = \Delta y_i^{\text{phys}} + b(p_1, p_2, \mathbf{x}_i) + \varepsilon_i, \qquad \varepsilon_i \sim \mathcal{N}\big(0, \sigma^2(p_1,p_2,\mathbf{x}_i)\big),$$

where $b$ is the systematic shift caused by the protocol switch, $\sigma^2$ is the extra measurement variance it introduces, and $\mathbf{x}_i$ are patient covariates that may change how acquisition affects segmentation, such as body size and contrast phase. A protocol is defined from image metadata: scanner model, reconstruction kernel and algorithm, slice thickness, and contrast phase. When physiology cannot have changed, so that $\Delta y^{\text{phys}} = 0$, the observed $\Delta y$ estimates $b$ and $\sigma^2$ directly.

We would build three sources of null pairs. The first is same-day or within-week scans with different protocols. In oncology these are common: a low-dose CT taken during PET/CT, paired with a contrast-enhanced diagnostic CT, or repeat reconstructions of one acquisition at different kernels and thicknesses, which many archives store side by side. The second is simulated pairs, where one raw acquisition is re-projected and reconstructed under alternative settings in the style of Flouris et al.. These cover transitions that real pairs rarely include. The third is a within-patient reference tissue. Following Borys et al.'s evidence that bone volume is stable over time, any apparent bone-volume jump at a protocol transition serves as an internal readout of acquisition bias. It is an auxiliary signal, not the primary estimate.

The function $b$ and the variance $\sigma^2$ are fitted with a hierarchical model that pools across related transitions. Rare scanner pairs then borrow strength from common ones, and the model shows wide uncertainty when a transition has never been observed. Per-patient trajectories are then fitted with a mixed-effects model over irregularly spaced scans. In that model each interval's change is corrected by $\hat b$ and weighted by the inverse of the total variance. This produces a corrected velocity and its standard error. A drift-aware minimal detectable change, $1.96\,\hat\sigma(p_1,p_2)$, sets the threshold for flagging wasting on a given pair of scans. The quantities we track are muscle volume, the Sarcopenia Index, visceral and subcutaneous fat volume, and mean muscle attenuation. The last is a proxy for fat infiltrating the muscle, which Borys et al. name as a gap in current volumetric phenotyping. Segmentation uses fixed public tools: TotalSegmentator-based pipelines and Comp2Comp.

Baselines

The naive reference is raw automated velocity. We run the same segmentation pipeline on every scan, compute the change in log volume per month, and ignore acquisition entirely. This is what anyone would do today with Comp2Comp or the BOA pipeline. The correction beats it if raw velocity shows significant nonzero change on null pairs while corrected velocity does not, and if corrected velocity improves prognostic performance on forward-in-time test years.

The strongest existing prognostic method is the baseline-only volumetric Sarcopenia Index of Borys et al., which reported HR 0.56 (abdominal CT) and 0.40 (thoracic CT) for survival and outperformed L3 muscle index and BMI. We recompute it on our cohort with the same segmenter and the same Cox and accelerated-failure-time specification. Velocity-based models must add to it, so every velocity model includes baseline SI. Beating it means a significant gain in time-dependent concordance and better calibration of 1- and 2-year survival over baseline SI plus clinical covariates, measured on patients whose scans come from years after the training period. No reported result was found on Lacuna for any longitudinal body-composition velocity model, so no published velocity number exists to compare against.

The strongest drift-handling competitor is cohort-level harmonization. It enters protocol indicators, or protocol-transition indicators, as fixed covariates in the trajectory model, which is equivalent to statistical batch correction of the extracted measures. It uses the same data and the same model family. It differs from our method only in that it estimates bias from the longitudinal cohort itself, with no null pairs and no transition-specific variance.

Two ablations isolate the key ingredient. One keeps the bias term $b$ but drops the variance term $\sigma^2$. The other fits $b$ from simulated pairs only or from real pairs only. These show whether the per-transition uncertainty, and not just the bias shift, is what reduces false alarms.

All models get the same tuning budget. They are selected on a validation window that precedes the test window in time, following the backtesting schedule of EMDOT.

Why not just…?

Why not just use a ratio like muscle-to-bone volume, which should cancel scanner scale effects? This is a real threat. The ratio cancels shifts that affect muscle and bone equally, such as changes in voxel spacing. Kernel and dose changes, however, move the soft-tissue and bone intensity thresholds differently, so the ratio need not cancel them. We test this directly: if the SI's null-pair bias and variance are already negligible, the correction adds nothing for SI. We would report that and restrict the method to fat depots and attenuation, where no stable denominator exists.

Why not just add scanner and kernel as covariates, the standard batch correction? When scanner changes are tangled with calendar time, treatment eras, and patient mix, covariates fitted on the longitudinal cohort absorb real population trends along with artifact. This is the "discard real signal" failure that Guo et al. (2022) describe for invariance methods. Covariates also say nothing about the individual-level noise that decides whether one patient's drop is real. Null pairs identify the artifact without this confounding. The covariate baseline and the variance-free ablation will show how much of the benefit comes from identification and how much from uncertainty.

Why not just make the segmenter scanner-invariant with domain adaptation, or fine-tune it on new scanners? The only large temporal test of these methods in the file, Guo et al. (2022), found no gain over standard training, although that evidence comes from tabular data. Fine-tuning also creates a new drift: the tool itself changes across a patient's timeline. We include one fine-tuned segmenter arm, adapted on unlabeled newer-scanner images, and measure its null-pair bias. If it removes the bias, output correction is unnecessary for that transition. The two approaches can also be combined.

Why not just resample every scan to a common slice thickness before segmenting? This addresses one parameter and leaves kernel, dose, and contrast untouched. We run it as a preprocessing arm and report its residual null-pair bias.

Proposed Experiments

The primary cohort must be a multi-year institutional archive with serial CT across at least one documented scanner replacement, similar to the 2004–2021 West German cohort in Borys et al.. The file lists no public longitudinal body-composition dataset, so gaining access to such an archive is the main practical risk. Two public sources play supporting roles. The FDG-PET-CT-Lesions dataset was acquired on a single scanner from 2014 to 2018 and serves as a within-scanner control, where estimated transition bias should be near zero. The serial CTs from the autoPET/CT IV longitudinal task used by Kirchhoff et al. serve as a second source of real acquisition pairs. For segmentation quality, the relevant reported figures are Comp2Comp's internal L3 Dice of 0.97 (muscle), 0.96 (visceral fat), and 0.97 (subcutaneous fat), with external Dice above 0.80 for muscle. These are cross-sectional accuracy figures and say nothing about the stability of change.

Four checks decide the question. The first quantifies the problem: on same-day null pairs, is raw apparent change in muscle and fat volume across protocol transitions significantly nonzero, and how large is it compared with published clinically meaningful wasting rates? If the bias and variance are tiny, the proposal ends there as a useful negative result. The second is an interrupted time-series test at each scanner installation date. Population-average raw trajectories should show a step at the switch, and corrected trajectories should not. The third is prognostic, run under EMDOT-style rolling backtesting (train through year $t$, test on later years). We compare corrected velocity plus baseline SI against raw velocity plus baseline SI, baseline SI alone, and covariate harmonization, using time-dependent concordance and calibration slope, since calibration is where Guo et al. (2021) found drift does the most damage. The fourth is clinical: among patients flagged as having lost at least 5% of muscle volume, what fraction of flags fall on protocol-transition intervals, and how much does the drift-aware minimal detectable change reduce that fraction without lowering the survival separation of flagged patients?