Brain-imaging studies of how memory changes between morning and evening ask a hard statistical question. Across hundreds of thousands of brain locations, where does the effect of a memory task differ between sessions? The difference being tested is small, since it is a difference of differences. There are very many locations to test. The standard safeguard, the Benjamini-Hochberg procedure for controlling the false discovery rate (the expected fraction of declared hits that are false), treats every location as equally likely to matter. That leaves real diurnal effects hard to find. Two false-memory studies run in morning and evening sessions, Fąfrowicz et al. and Ceglarek et al., faced exactly this problem. Fąfrowicz et al. openly note that they chose a correction less strict than family-wise control, since the stricter one would erase their evening-specific findings. Nobody can currently say how many of those findings are real.
This proposal rests on one observation. In a design where each person is scanned in both sessions, the pooled task map (morning plus evening) contains information about where diurnal effects are likely. Under the null of no time-of-day effect, that map is also statistically independent of the time-of-day contrast (morning minus evening). The pooled map can therefore guide the diurnal test by ranking, filtering, or weighting locations. The resulting p-values stay exactly valid, because they come from sign-flip permutation, which re-randomizes which session is labelled morning within each person. We will turn this into a working procedure and state precisely when its guarantee holds. We will then find out, on semi-synthetic and real diurnal memory fMRI, whether soft weighting beats a simple mask and whether either beats the flat and spatial corrections now in use.
Core Claim
For subject $i$ and brain location $v$, let $m_{iv}$ and $e_{iv}$ be the task-contrast estimates (for example, correct rejection of lures minus false alarms) in the morning and evening sessions. Let $s_{iv}=m_{iv}+e_{iv}$ be the pooled effect and $d_{iv}=m_{iv}-e_{iv}$ the diurnal difference. Then
$$\mathrm{Cov}(s_{iv}, d_{iv}) = \mathrm{Var}(m_{iv}) - \mathrm{Var}(e_{iv}),$$
which follows from expanding the product. The two are uncorrelated whenever the two sessions are equally noisy.
A stronger statement is what the method needs. Suppose each subject's whole-brain pair of maps is exchangeable under the null, meaning swapping the morning and evening labels leaves its joint distribution unchanged. Then, conditional on every pooled map, flipping the sign of each subject's difference map is a valid null randomization. This holds with arbitrary spatial dependence, because the flip applies to the whole brain at once. So any covariate computed only from the pooled maps can be used freely. Examples are its magnitude at each location, a spatially smoothed version, or network membership taken from an independent-component decomposition of the pooled data. None of these touches the permutation validity of the diurnal p-values.
Covariates are turned into weights $w_v \ge 0$ that average to one. The weighted Benjamini-Hochberg rule then rejects the $k$ smallest values of $p_v/w_v$, where
$$k=\max\{j : p_{(j)}/w_{(j)} \le j\alpha/V\}$$
and $V$ is the number of locations tested.
The claim has two parts. First, this recovers more true diurnal effects than flat correction at the same nominal false discovery rate. Second, it controls that rate at least as well as spatial empirical-Bayes smoothing does. The gain depends on an empirical premise: diurnal changes concentrate where the task does something. The premise is plausible, since the default-mode deactivation differences Fąfrowicz et al. report sit in a strongly task-modulated network. But it is not guaranteed, and the experiments test it directly.
The closest prior work runs in two lines. The first uses covariates to raise power. Contextual online FDR control learns weights from side information and reports 10% more discoveries on Airway RNA-Seq and a 51% power gain on a diabetes cohort. NeurT-FDR feeds test-level features into a learned prior. Both assume the covariate is independent of the null p-values and take that assumption from outside the data.
The second line exploits spatial structure. False discovery rate smoothing lets the prior probability of signal vary smoothly across a 1.23-million-voxel working-memory map. It borrows strength from neighbouring values of the same statistic being tested, and it has no finite-sample guarantee.
Our proposal differs from both lines. The covariate comes from the experiment itself, through a decomposition that makes it independent by design, and validity is a permutation argument rather than a modelling assumption. We also do not propose continuous circadian-phase covariates. The available data have only two sessions, so that direction cannot be tested here.
Research Program
The first component is the procedure and its guarantee. We will write out the conditional sign-flip argument and state exactly what the null must be. The null is exchangeability of the full session pair, not merely equal means. Two things can break the independence. The first is a difference in variance between sessions, for example an evening session noisier from motion or fatigue; the file notes that fatigue was not measured in these studies. The second is a session-order effect that is not counterbalanced.
For each failure we will build a remedy and a diagnostic. The remedy for variance differences is to standardize each subject's session maps by their residual noise before forming the pooled and difference maps. The diagnostic is a test of whether the covariate predicts the size of the difference map in locations where effects are known to be null.
We will also check whether weighted Benjamini-Hochberg on positively dependent fMRI statistics needs a dependence-robust fallback. Two candidates are the weighted Benjamini-Yekutieli rule, whose role under correlated errors is discussed in CiteGuard, and e-value based testing (compound e-values code).
The second component is a family of weight designs, ordered by complexity. The simplest is a hard mask on pooled effect size. Next are soft monotone weights on the absolute pooled statistic, with a floor so that locations with no pooled effect keep some chance of rejection. Next are the same weights after spatial smoothing of the pooled map. The richest design adds network labels from independent-component analysis of the pooled data. Because the weights never look at the difference maps, all of these share the same guarantee.
The third component is a semi-synthetic testbed that fixes the ground truth. We start from real subject-level maps and assign session labels at random, which creates a true global null for the diurnal effect. We then plant diurnal effects of controlled size in chosen regions. The key setting varies how much the planted effects overlap with task-active regions, from full overlap to none.
The hardest case is a crossover. There, a region activates in the morning and deactivates in the evening, so its pooled effect is near zero and the covariate points away from it. This case bounds how badly the method can fail when its premise is wrong.
Baselines
The naive reference point is flat Benjamini-Hochberg on the voxel-wise diurnal contrast, the procedure used by Fąfrowicz et al.. It is what the field does now. Any method that cannot beat it on power at matched false discovery rate is not worth adopting. It will be run on the same subject-level maps with the same sign-flip p-values as every other method, so that p-value construction is identical across methods and only the multiplicity rule differs.
The strongest existing competitor is false discovery rate smoothing, applied directly to the diurnal statistic map on the voxel adjacency graph. It is the only method in the file shown on whole-brain fMRI to produce contiguous clusters where flat correction gave scattered noise. It will receive the same maps and a tuning budget for its penalty strength equal to the budget we give our weight shape, with both selected on held-out semi-synthetic replicates.
No reported number was found on Lacuna for its true-positive rate or empirical false discovery rate on real fMRI. The paper reports only qualitative cluster maps on the 1.23-million-voxel dataset, plus simulation results without figures in the file. We will therefore reproduce it rather than quote it. Beating it means two things together: at least as many true detections at a nominal 5% rate on the semi-synthetic testbed, and an empirical rate that stays at or below nominal in the global-null and variance-mismatch settings, where we expect smoothing to overshoot.
The ablations isolate the key ingredient. The first is the hard pooled-effect mask followed by flat correction within it, the simplest use of the same independence principle. The second uses the same soft weights computed from a deliberately invalid source: the absolute diurnal statistic itself, smoothed. This shows what happens to error control when independence is abandoned. It separates the benefit of "any spatial prior" from the benefit of "an independent prior." Covariate weighting on its own, whether in the style of CwLORD++ or NeurT-FDR, has reported gains in the file (10% more discoveries on Airway RNA-Seq, 51% more power on the diabetes cohort). Those gains are on genomics and clinical data, not imaging, so they set an expectation for effect size and are not a direct comparison.
Why not just…?
Why not just use flat Benjamini-Hochberg, as published studies do? It is valid under positive dependence and needs no modelling. Its cost is power. On whole-brain working-memory data it produced scattered, uninterpretable hits, according to the FDR smoothing paper. The semi-synthetic power curves will show how many planted diurnal effects it misses relative to weighted variants. If the gap is small, the correct conclusion is that current practice is adequate, and we will report that.
Why not just mask to regions with a strong pooled task effect and correct within the mask? This is the real threat. It uses the same independence principle and may capture most of the gain. We treat it as a first-class candidate, not a straw man. If soft weights do not beat it by a meaningful margin across overlap settings, the recommendation becomes "mask by the independent pooled map," and the contribution narrows to establishing when that mask is valid. The case where soft weights should win is partial overlap and crossover effects. A hard mask discards those locations entirely, while a weight floor keeps them testable. The experiments measure exactly that difference.
Why not just restrict analysis to an anatomical region of interest such as the hippocampus? The diurnal effects reported so far sit outside any single anatomical hypothesis. They involve default-mode and medial visual networks, right lingual gyrus and left cerebellum in Fąfrowicz et al.. They also include opposite-signed hippocampal and supplementary motor effects in Ceglarek et al.. An a priori mask would have missed most of these. The data-derived pooled map adapts to wherever the task acts without the analyst choosing regions.
Why not just apply spatial FDR smoothing to the diurnal map? Smoothing borrows strength from the very statistic under test and lacks a finite-sample guarantee. Its penalty is also known to shrink small local peaks toward the global mean, which is the regime subtle diurnal effects occupy. The global-null and variance-mismatch experiments will show whether this translates into error inflation or power loss. If smoothing controls error and matches power, the two approaches can be combined by using the smoothed pooled map as the weight source, which is one of our planned variants.
Proposed Experiments
The semi-synthetic study uses real subject maps. The DRM diurnal fMRI data (58 subjects in Fąfrowicz et al., 54 in Ceglarek et al.) serve if the authors grant access. The cross-sectional spatial working-memory dataset from the FDR smoothing paper is the fallback, with runs split into pseudo-sessions. The design crosses planted effect size, overlap with the task map, crossover fraction, and an injected variance mismatch between sessions. Metrics are empirical false discovery rate, true-positive rate, and spatial accuracy of the detected region, averaged over repeated random session labellings.
The decisive checks are as follows. First, every method built on the pooled covariate must hold the empirical rate at or below the nominal 5% under the global null. Under variance mismatch, it must fail without standardization and recover with it; failing to recover would falsify the practical guarantee. Second, under full and partial overlap, soft weights should exceed flat correction on power. Third, under pure crossover, the weight floor should keep power loss relative to flat correction small, and we will state the loss honestly.
We then apply the procedures to the real DRM contrasts. At the voxel level, the contrast is correct rejection of lures versus false alarms, by session. At the region level, it is Ceglarek et al.'s 90-region co-activation effects crossed with phase and probe type, where multiplicity is smaller but still substantial. We ask whether the published evening-specific lingual and cerebellar effects survive under each method. We also ask whether new effects appear, and whether split-half replication across subjects agrees more often for weighted discoveries than for flat ones.
This design has a stated limitation. It cannot separate circadian phase from hours awake, and the file's own open problems note that separating them needs fatigue measures that these datasets lack.
References
- Dynamics of working memory process revealed by independent component analysis in an fMRI study
- Non-linear Functional Brain Co-activations in Short-Term Memory Distortion Tasks
- Contextual Online False Discovery Rate Control
- Probabilistic Model Incorporating Auxiliary Covariates to Control FDR
- False Discovery Rate Smoothing
- CiteGuard: Conformal False-Discovery Control for Faithful Retrieval-Augmented Generation