Immune checkpoint drugs help only a minority of cancer patients. The tissue tests used to choose who gets them, mainly a stain for the protein PD-L1, often predict response barely better than chance. The usual fix is to measure more: more proteins, more image features, more omic layers. Computational neuroscience has a sharp result about when this strategy fails. When many neurons are read together, adding neurons improves the readout only if their trial-to-trial fluctuations, the "noise," do not line up with the direction that separates the stimuli. If the fluctuations do line up, the information saturates no matter how many neurons are added. We propose to carry this test into cancer biomarkers. We treat the regions of one patient's tumor as repeated "trials" of that patient's state. We treat response versus non-response as the "stimulus." We then ask how much of biomarker failure comes from three sources. The first is sampling noise, which more biopsy regions would average away. The second is shared noise aligned with the response direction, which no amount of extra measurement from the same tissue can fix. The third is a genuine absence of signal.
The practical payoff is a diagnosis rather than another classifier. The answer tells a clinical team whether to spend its next dollar on more markers per slide, more cores per patient, or a different kind of measurement. Examples of the last option are blood inflammation indices or on-treatment scans, which carry information that breaks the shared noise. We also test a mechanistic guess: the aligned noise component is partly systemic host inflammation. If so, conditioning on a routine blood count should lift the ceiling that additional tissue markers cannot.
Core Claim
Standard biomarker pipelines assume independent noise in two places, usually without saying so. First, they average marker densities across tiles or regions as if each region were an independent draw. That treats regions as having independent noise. Second, they combine markers as if each contributed separate evidence. That treats markers as having independent noise. Both assumptions are testable. When either fails in a particular geometry, response discriminability hits a hard ceiling. Our claim is that measurable, response-aligned shared noise explains a substantial part of the "predictive leakage" documented for PD-L1 and related scores (Implications of the tumor immune microenvironment for staging and therapeutics). The claim is falsifiable. Discriminability should saturate as regions and markers are added, at a level predicted by the estimated aligned noise component.
The key quantity is linear discriminability between responders and non-responders, $d'^2 = \Delta\mu^\top \Sigma^{-1} \Delta\mu$. Here $\Delta\mu$ is the difference in mean marker profile between the two outcome groups, and $\Sigma$ is the covariance of profiles within an outcome group. Suppose $\Sigma$ contains a component $\varepsilon\, \Delta\mu \Delta\mu^\top$, that is, fluctuations of size $\varepsilon$ along the very direction that separates the groups. Then $d'^2$ is bounded by $1/\varepsilon$ however many markers are measured. This follows from the matrix inversion identity applied to a rank-one addition.
The region axis has its own version of the bound. If the region-to-region fluctuations of a tumor's marker value have variance $\sigma^2$ and a correlation $\rho$ shared across regions, the variance of an $n$-region average is
$$\sigma^2\left(\rho + \frac{1-\rho}{n}\right).$$
This variance stops shrinking once $n$ exceeds roughly $1/\rho$. Slide-wide staining shifts, tumor-wide fibrosis, and systemic inflammation are natural sources of $\rho$ and $\varepsilon$.
How This Relates to Prior Work
The neuroscience side supplies the concepts and one important constraint. An Estimation-Theoretic Framework for the Presentation of Multiple Stimuli shows that the alignment between noise and the signal direction decides whether correlations hurt or help coding. That alignment is the quantity we estimate. Bridging neuronal correlations and dimensionality reduction separates signal correlation (similar average responses across conditions) from noise correlation (shared fluctuations within a condition). We apply that distinction to cell-type co-occurrence in tissue.
Population Decoding Based on an Unfaithful Model works in the opposite direction. It proves that a decoder ignoring correlations can match the faithful one, at about one fifth the compute. The proof requires symmetric tuning and uniformly spread preferences, conditions tumor markers plainly violate. We treat its result as a hypothesis to test: in tissue, does the independent decoder lose anything, and by how much?
DeCorrNet supplies a method we will also test. It adds a loss that suppresses within-condition correlation in brain–computer interface decoders, raising monkey reaching accuracy from 73.1% to 85.5% with a support vector machine. We differ in two ways. DeCorrNet removes noise to boost accuracy; we measure the noise to explain a ceiling. And its "trials" are true repeats, whereas ours are spatial replicates within a patient.
The oncology side motivates the problem and supplies the data. The pathomics ensemble model PDEM, CT radiomics of immune status, biology-guided deep learning and SimTA serial modeling all improve on PD-L1 by concatenating features. None of them asks whether the residual error is sampling noise or response-aligned shared noise.
HEX virtual spatial proteomics is the enabling tool. It predicts 40 protein markers from ordinary H&E slides (H&E is the standard pink-and-purple tissue stain), with an average Pearson correlation of 0.790. That gives many regions per patient at low cost, which our region-as-trial design needs. Noise regularization for single-cell RNA-seq is a warning about our own estimator. Preprocessing itself creates correlations, so we must check that the estimated $\rho$ and $\varepsilon$ are not artifacts of normalization or of HEX's imputation. Finally, the host-factor literature motivates the inflammation hypothesis. That literature includes the SITC review, the CONFIRM trial analysis of constitutive inflammation, and serum antibody profiles.
Research Program
We first build a hierarchical covariance estimator for tissue profiles. It separates three covariance pieces: within-patient region-to-region covariance across markers, its shared cross-region part $\rho$, and between-patient covariance within each outcome group. From these it computes cross-validated, bias-corrected $d'^2$ and the aligned fraction $\varepsilon$. Bias correction matters here, because naive plug-in $d'^2$ is strongly inflated when there are 40 markers and about 150 patients. Shrinkage covariance and held-out estimation of $\Delta\mu$ handle this.
The estimator is first validated on synthetic populations of the kind used by Wu et al. We then deliberately break the symmetry with skewed, zero-inflated "markers" and plant a known $\varepsilon$, so that recovery can be scored against ground truth. As a cross-domain sanity check, we run the same estimator on the monkey center-out reaching data used by DeCorrNet. Repeated trials there give a true noise covariance against which our region-as-trial approximation can be compared.
Next, we apply the estimator to lung cancer. We use measured CODEX multiplex proteins (CODEX is a method for imaging dozens of proteins in one tissue section) where the Stanford-TMA and Stanford-WSI resources provide multiple cores or regions per patient. We use HEX-imputed markers on whole slides for TCGA-LUNG and for the 148-patient Stanford-IO cohort of patients treated with checkpoint drugs. For each cohort we trace two saturation curves: $d'^2$ and AUC (area under the ROC curve) against number of regions, and against number of markers. We then fit both to the bounds above. Finally, we test the mechanism. We add blood neutrophil-to-lymphocyte ratio or a related systemic index as a conditioning variable and ask whether $\varepsilon$ falls and the ceiling rises.
Baselines
The naive reference point is PD-L1 alone, together with tumor mutational burden where available. PDEM reports PD-L1 combined positive score AUCs of only 0.45 to 0.58 in gastric cancer. Every method must clear this floor on our cohorts, evaluated with the same splits.
The strongest existing method on our main cohort is HEX features fused with morphology through MICA, the co-attention model from HEX. That paper reports a 24–39% gain in immunotherapy response prediction over PD-L1 and TMB on Stanford-IO. The file gives this only as a relative improvement: no reported absolute AUC was found on Lacuna for HEX/MICA on Stanford-IO. We will therefore retrain it on our identical outer cross-validation folds, with the same tuning budget, and report its AUC ourselves. On gastric data, should we obtain access, the reference is PDEM's external AUC of 0.914–0.927.
The concatenation baseline is a LASSO or random-forest model on region-averaged markers, as in PDEM and the radiomics score. It gets the same nested cross-validation as everything else.
The ablation that isolates the key ingredient pits two decoders against each other on identical features. One is an independent-noise decoder: Gaussian naive Bayes with region averaging, playing the role of Wu et al.'s unfaithful model. The other is a faithful decoder: shrinkage linear discriminant analysis with covariance-weighted region pooling. We also run a DeCorrNet-style decorrelation loss adapted to patients, with outcome class as "task" and regions as "trials."
Beating the baselines is not mainly about AUC. The proposal succeeds if three things hold together. The estimated $\varepsilon$ and $\rho$, computed on training folds, must predict on held-out folds where each saturation curve flattens. The gap between faithful and independent decoders must track the estimated alignment across cohorts. And the conditioning variable must raise held-out AUC above the HEX/MICA retrain.
Why not just…?
Why not just use LASSO or a random forest, which already handles correlated features? For prediction alone, that may be enough, and we expect it to roughly tie the faithful decoder in AUC. What LASSO cannot do is say whether a dropped feature was redundant signal or shared noise. It also cannot predict whether a second biopsy would help. The saturation-curve experiments answer that question, and LASSO is run on exactly the same curves for comparison.
Why not just call the faithful decoder linear discriminant analysis and stop? This is the most serious objection, and it is correct. Our faithful decoder is shrinkage linear discriminant analysis, and we claim no new classifier. The contribution is the decomposition. It splits within-class covariance into region-level and patient-level parts, isolates the response-aligned fraction, and links it to a measurable host variable. If the aligned fraction turns out negligible in every cohort, the honest conclusion is that biomarker failure is sampling-limited or signal-limited, and we will report that.
Why not just use a larger foundation model? HEX already needed 819,000 paired tiles. If $\varepsilon$ is real and comes from tissue-wide shared fluctuation, a richer representation of the same tissue inherits the same ceiling. We test this directly by computing $\varepsilon$ on foundation-model embeddings as well as on the 40 markers.
Why not just batch-correct the data? Correction of the kind used for single-cell RNA-seq removes technical correlation. It cannot remove biological shared noise such as systemic inflammation without also removing signal. We will run the analysis before and after slide-level stain normalization. If $\varepsilon$ disappears after normalization, the noise was technical, which is still a useful and actionable finding.
Decisive Checks
The program rests on four checks. First, on synthetic data, the estimator must recover planted $\varepsilon$ and $\rho$ under skewed, asymmetric markers, and it must show the independent decoder failing exactly where Wu et al.'s symmetry assumptions break. Second, on Stanford-TMA, Stanford-WSI and TCGA-LUNG, AUC against region count must follow the $\rho + (1-\rho)/n$ form, with $\rho$ fit on training folds. Third, on Stanford-IO, AUC against marker count must plateau near the $1/\varepsilon$ bound, and conditioning on systemic inflammation must shift that plateau upward. Fourth, every result must survive a control in which HEX-imputed markers are replaced by measured CODEX markers where both exist, so that we know the shared noise is not created by the imputation model.
If the curves do not saturate, the conclusion is that current biomarkers are sampling-limited and need more cores rather than more markers, which is itself a clinically useful answer.
References
- Implications of the tumor immune microenvironment for staging and therapeutics
- An Estimation-Theoretic Framework for the Presentation of Multiple Stimuli
- Bridging neuronal correlations and dimensionality reduction
- Population Decoding Based on an Unfaithful Model
- DeCorrNet: Enhancing Neural Decoding Performance by Eliminating Correlations in Noise
- Development and interpretation of a pathomics-driven ensemble model for predicting the response to immunotherapy in gastric cancer
- Noninvasive imaging of the tumor immune microenvironment correlates with response to immunotherapy in gastric cancer
- Biology-guided deep learning predicts prognosis and cancer immunotherapy response
- A multi-omics-based serial deep learning approach to predict clinical outcomes of single-agent anti-PD-1/PD-L1 immunotherapy in advanced stage non-small-cell lung cancer.
- AI-enabled virtual spatial proteomics from histopathology for interpretable biomarker discovery in lung cancer
- Noise regularization removes correlation artifacts in single-cell RNA-seq data preprocessing
- Advances in the understanding and therapeutic manipulation of cancer immune responsiveness: a Society for Immunotherapy of Cancer (SITC) review
- Constitutive inflammation and epithelial-mesenchymal transition dictate sensitivity to nivolumab in CONFIRM: a placebo-controlled, randomised phase III trial
- Antecedent viral immunization and efficacy of immune checkpoint blockade: an extensive serum antibody profile to predict outcomes in non-small cell lung cancer