Three Fast Scans or One Slow One? Budgeting MRI Time to Shorten the Follow-Up Needed for Volumetric Change

A patient's brain atrophy can only be confirmed when the measured change between two visits is larger than the noise in measuring volume. That noise has two sources: the scan, which is corrupted by motion, noise and reconstruction artifacts, and the automated segmentation model that turns the scan into a volume. The more noise there is, the longer clinicians must wait before a real change can be distinguished from measurement error. Many studies stop at 6 months or a year, and so they end before the change they care about becomes detectable.

Ultra-fast MRI changes what one scanner slot can buy. A standard 3D T1-weighted brain scan (MPRAGE) takes over 5 minutes. An accelerated version (Wave-CAIPI, a parallel-imaging scheme that shortens acquisition by spreading aliasing more evenly) takes about a minute and a half. In the time of one slow scan, a clinic can therefore acquire three fast ones. We propose to test whether averaging automated volumes from several fast same-session scans reduces measurement error enough to shorten the minimum follow-up needed to detect individual atrophy. The answer depends on a quantity nobody has measured: what fraction of a segmentation pipeline's error is independent across near-identical repeat scans, and so shrinks with averaging, and what fraction is shared, and so does not.

Core Claim

The reliability of an automated volumetric biomarker should be reported in units of time: the minimum follow-up interval at which an individual's expected change exceeds measurement error. That interval depends on how measurement error splits into parts that averaging can remove and parts it cannot. Suppose $\sigma_{\text{ind}}$ is the per-scan error that varies independently across repeats within a session, and $\sigma_{\text{sys}}$ is error shared across repeats within a session but differing between sessions. Shared error includes head positioning, hydration and a segmentation model's consistent misreading of that session's contrast. With $k$ repeats averaged per visit and a true rate of change $r$ (for example mL/year of hippocampal loss), the minimum detectable follow-up is

$$T_{\min}(k) = \frac{z\sqrt{2}\,\sqrt{\sigma_{\text{sys}}^2 + \sigma_{\text{ind}}^2/k}}{|r|} + \frac{|\delta|}{|r|}\,\mathbb{1}[\text{protocol changes between visits}],$$

where $z$ is the normal quantile for the chosen confidence level. The $\sqrt{2}$ appears because a change score differences two noisy visits. The term $\delta$ is the systematic offset between fast and standard protocols, and it adds to the interval whenever a patient switches protocols mid-follow-up.

The equation makes three testable predictions. First, fast repeats help only if $\sigma_{\text{ind}}$ dominates $\sigma_{\text{sys}}$. Second, a segmentation model can be trained to shrink $\sigma_{\text{ind}}$ but not $\sigma_{\text{sys}}$. Third, the protocol offsets already observed for brain-age pipelines would, for volumes, translate directly into months of added follow-up for patients who switch sequences.

What Prior Work Establishes and Leaves Open

The closest work is Ultra-fast MRI for brain-age prediction in a real-world cognitive disorders clinic. It paired Wave-CAIPI and standard MPRAGE in 147 clinic patients and found cross-protocol absolute-agreement intraclass correlation (ICC-AA) typically above 0.90 across six brain-age pipelines. The intraclass correlation coefficient (ICC) is the share of total variance that comes from true differences between subjects rather than from measurement error. The same study also found pipeline-specific offsets and acquisition-by-diagnosis interactions. This work motivates ours: it shows fast scans agree with slow ones on average. It does not treat the time saved as a resource to spend on repeats. It does not examine segmented regional volumes. It tested scan-rescan stability only in 15 people, with no longitudinal follow-up.

Two papers constrain the design. Volumetric assessment of extracranial carotid artery aneurysms combined ICC above 0.94 with Bland-Altman analysis to set a 2 mL threshold for true growth. That is the right template of converting reliability into a detectable-change threshold, but it used manual tracing at 49 minutes per scan. The methodological review Quantifying Measurement Reliability and Consistency separates absolute agreement ($\text{ICC}_{2,1}$) from consistency ($\text{ICC}_{3,1}$). The research file also notes that ICC depends on how varied the cohort is. For that reason we report standard error of measurement and $T_{\min}$ as primary outcomes and ICC only as a secondary one.

Two lines of work reduce longitudinal segmentation noise in other ways. Temporally Consistent Segmentation of Brain Tissue From Longitudinal MR Data couples timepoints in a 4D fuzzy-clustering formulation, cutting label reversals from over 2% (FSL FAST) to under 0.6% on the Baltimore Longitudinal Study of Aging (BLSA). The LSOR codebase similarly enforces feature consistency across visits. Both need multiple visits and smooth across them. That is precisely what cannot be relied on when follow-up is short, and smoothing risks shrinking true change along with noise. Our approach reduces noise within a visit instead.

Temporal Conditioning for Longitudinal Brain MRI Registration and Aging Analysis takes a third route: TimeFlow extrapolates future anatomy from two scans. That is prediction, not measurement, and it cannot certify that a given patient has changed.

Research Program

The first component is a prospective acquisition study in a memory clinic, modeled on the Queen Square protocol. At each visit, every participant receives one standard MPRAGE and three Wave-CAIPI scans, with repositioning between two of the fast scans. This lets repositioning error be separated from pure acquisition noise. A second visit one to two weeks later, during which no biological change is expected, provides between-session error. A third visit at 12 months provides real change.

Automated volumes of hippocampus, lateral ventricles and whole brain are computed with an off-the-shelf 3D segmenter, the TransUNet codebase (Beckschen/TransUNet), and with FSL FAST. A nested random-effects model then estimates $\sigma_{\text{ind}}$, $\sigma_{\text{sys}}$ and $\delta$ separately for each structure and each pipeline.

The second component is a training intervention aimed only at $\sigma_{\text{ind}}$. Same-session fast repeats are natural pairs with identical anatomy. We fine-tune the segmenter with a penalty on the within-subject variance of predicted volumes across the repeats, divided by the between-subject variance in the batch. The division matters. A plain penalty on volume differences can be satisfied by pulling every prediction toward the population mean, which destroys the between-subject signal. The ICC-shaped ratio penalizes that collapse. We do not claim this is a general differentiable ICC. It is the smallest loss that targets the right error component, and an ablation tests the plain difference loss directly.

The third component converts the error estimates into $T_{\min}$. Rates $r$ come from longitudinal ADNI and OASIS trajectories for diagnostic subgroups. Each estimate of $T_{\min}$ is then checked against the 12-month visit: we count how many patients cross the detection threshold at 12 months, and see whether that count agrees with what the estimate predicts.

Baselines

The naive reference is current practice: one standard MPRAGE per visit, segmented independently at each visit, with change computed as the difference in volume. Its $T_{\min}$ is the number to beat. Reporting it for hippocampal and ventricular volume is useful on its own, because we found no reported result on Lacuna for scan-rescan error of automated hippocampal volumes under Wave-CAIPI.

The strongest existing competitor for longitudinal stability is the 4D temporally consistent formulation of Li et al. It reports a label-reverse rate below 0.6%, against over 2% for FAST, and temporal consistency of 96.4% for gray matter and 98.1% for white matter on BLSA, according to Temporally Consistent Segmentation of Brain Tissue From Longitudinal MR Data. We run it on the same visits, using only the standard scan, as a within-subject longitudinal pipeline. Beating it means a lower $T_{\min}$ for a fixed scan budget, with no underestimation of true 12-month change. The latter check matters because a method that shrinks change estimates also shrinks apparent error. For brain-age agreement, the reference point is ICC-AA typically above 0.90 from Ultra-fast MRI for brain-age prediction in a real-world cognitive disorders clinic. We report the corresponding $\text{ICC}_{2,1}$ for volumes, noting that the numbers are not directly comparable because the cohorts differ.

Three ablations isolate each ingredient. The first uses three fast repeats with no consistency fine-tuning, which isolates averaging. The second uses one fast scan with fine-tuning, which isolates the loss. The third uses a plain volume-difference loss in place of the variance ratio, which tests whether the normalization matters.

Every arm uses the same participants, the same pretrained initialization and the same fine-tuning budget. Hyperparameters are tuned only on a held-out subset of subjects.

Why not just…?

Why not just use the full slow scan and a better segmenter? This may win, and the study is designed to show whether it does. If $\sigma_{\text{sys}}$ dominates, averaging cannot help. In that case the slow scan's higher signal-to-noise ratio per scan will give the lower $T_{\min}$, and the decomposition will say so directly. What the variance decomposition adds is knowing which error to attack. The concern about acquisition-by-diagnosis interactions in Ultra-fast MRI for brain-age prediction in a real-world cognitive disorders clinic runs against fast scans, so we estimate $\delta$ separately within each diagnostic group.

Why not just use a longitudinally coupled method like Li et al. or LSOR? These are a genuine threat when there are many visits. With only two or three visits, coupling has little to borrow from. Coupling can also bias estimated change toward zero, which makes apparent error look smaller than it is. The 12-month comparison of estimated against expected change detects that bias. The two approaches are also complementary: a hybrid arm feeds same-session averaged volumes into the coupled model.

Why not just average the three images and segment once? Averaging images removes acquisition noise before segmentation. Averaging volumes also removes segmentation noise that varies between repeats. Both are run. If image averaging matches volume averaging, the segmentation model contributes little independent error, and the fine-tuning component is unnecessary. We would then drop it.

Why not just report ICC? ICC rises in heterogeneous cohorts regardless of how precise the measurement is. A memory clinic and a healthy-aging cohort would therefore rank the same pipeline differently. $T_{\min}$ is tied to a specific clinical question and a specific rate of change, so it does not have this problem. ICC is reported alongside it for comparability.

Decisive Checks

The central test is whether $T_{\min}(3)$ with fast scans falls below $T_{\min}(1)$ with the standard scan for hippocampal volume. The observed fraction of patients crossing the threshold at 12 months must match the prediction within its confidence interval. If $\sigma_{\text{sys}}/\sigma_{\text{ind}}$ turns out to exceed about 1, averaging three scans reduces total error by less than about 15%. We would then report that fast repeats do not buy shorter follow-up, which is a useful negative result for clinic scheduling. A second check is whether $\delta$ between protocols, converted to months via $|\delta|/|r|$, exceeds the follow-up savings. If it does, patients must never switch protocols between visits.

The main risk is the small test-retest cohort. We size it by power for estimating a variance ratio rather than for detecting a difference in means. We also pre-register that result and the $T_{\min}$ comparison as the primary endpoints.