Sampling-Aware Labels for Multi-Task Cancer Staging

Models that predict a cancer's stage before surgery learn from the pathology report written after surgery. The pathology report is not a clean answer key. Whether a patient is recorded as "node-negative" depends partly on how many lymph nodes the surgeon removed and the pathologist examined. Remove too few, and real metastases go unseen. Clinicians call this stage migration. For esophageal cancer, Yuan et al. find that survival keeps improving up to about 18 examined nodes, with a hazard ratio of 0.98 per additional node. Below that number, a "node-negative" label is partly a statement about surgical thoroughness. A model trained to predict tumor extent (T), nodal spread (N) and distant spread (M) together therefore receives an N signal that is systematically wrong in one direction, and wrong more often for some patients than for others.

We propose that a meaningful share of what looks like multi-task interference in staging models is this label corruption. Interference here means a shared network getting worse at one task because it is also trained on another. The concrete claim has two parts. First, the per-patient count of examined nodes, which is recorded in public registries, can be built into the training loss as a model of how likely a true metastasis was to be missed. Second, once the nodal labels are corrected this way, the gradient-balancing machinery usually brought in to fix multi-task conflict adds little. The work is built on public data with a released benchmark, so that, unlike most staging results, it can be checked by others.

Core Claim

The nearest existing work is Wang et al.. They trained a shared network with four output heads, predicting stage, histology, grade and lymph node metastasis in cervical cancer from 14 preoperative clinical features. Multi-task training beat single-task models on stage, grade and histology. Lymph node metastasis was the exception: it stalled at 76% accuracy and did not beat single-task learning. The authors attributed this to class imbalance and shared-parameter interference. The research file frames the natural follow-up as applying conflict-avoiding optimizers to full TNM staging. Two such optimizers are M2ASR, which reweights tasks dynamically by gradient conflict using a stochastic multi-objective method called MoDo, and ETR-NLP, which routes each task through its own partly separate parameters. We think that follow-up treats a symptom.

Interference in speech has a clear mechanism: recognizing words requires discarding speaker identity, while identifying speakers requires keeping it. Adi and Collobert's comparison shows deep layers shedding speaker information. Wu et al. show that detecting speaker changes and recognizing words pull against each other. In tabular or registry-based staging there is no comparably strong reason for T and N to compete. Both reflect how aggressive the same tumor is. A more economical explanation for the stalled N head is that roughly one class of its labels, pN0 with few nodes examined, is contaminated. The contaminated examples push shared features away from the signals that also predict T.

What is new here is not modeling stage migration in general. LODDS (the log odds of positive versus negative examined nodes) and the positive-node ratio already adjust for it. Those adjustments, however, are computed after surgery and used as prognostic variables, not as training targets. Our contribution is to turn the examined-node count into a per-example label-reliability model inside the training loss of a preoperative multi-task predictor. We then test directly whether doing so removes the measured gradient conflict.

Research Program

Let $p$ be the model's predicted probability, computed from preoperative features only, that the patient truly has nodal metastasis. Let $k$ be the number of nodes later examined, a quantity used only during training. Let $\pi_\theta(k)$ be a learned, monotonically increasing probability that a true metastasis is detected when $k$ nodes are examined. A simple parametric form is $1-e^{-\lambda k}$, and we will also fit a monotone spline. The nodal head is trained with the likelihood

$$ P(\text{pN+}) = p\,\pi_\theta(k), \qquad P(\text{pN0}) = (1-p) + p\,(1-\pi_\theta(k)), $$

so a node-negative label from a sparse dissection costs the model little when it predicts positivity, while the same label from a thorough dissection costs it a lot. At test time the model outputs $p$, the estimate of true nodal status, which is the quantity a clinician needs before deciding on surgery or neoadjuvant therapy.

The detection curve is not identified from binary labels alone, so we constrain it in two ways. The first is monotonicity. The second uses the count of positive nodes among pN+ patients: how that count is distributed at different $k$ tells us how often small nodal burdens would be missed.

The T, N and M heads share a trunk. We first study tabular preoperative features. We then add an imaging arm, which serves only as a negative control (see below).

Reproducibility is a design constraint, not an afterthought. Every primary claim is made on the public SEER registry, using the esophageal setting of Yuan et al. and the resectable pancreatic head setting of Zou et al.. We release a written specification of which registry fields count as "known before surgery", along with fixed splits, code and evaluation scripts. Private-cohort papers such as Wang et al. or Devnath et al., whose results cannot be audited, could then report on a common open task. We also hold out whole registry sites as test sets, mimicking multi-center shift. The federated lymph-node study did not test this kind of shift, because it split one hospital's data into artificial clients.

For imaging, we use RADCURE, a public head and neck CT cohort of 1,570 patients. There, Kazmierski and Haibe-Kains model the tumor and individual nodes as a graph and predict distant metastasis. RADCURE patients were treated largely without surgical nodal dissection, so their nodal labels carry no sampling-driven corruption. If our account is right, the sampling-aware loss should give no benefit on RADCURE, and any interference that remains there must have a different cause, such as the fine-detail-versus-coarse-shape tension the file hypothesizes for small nodes. That is a falsifiable control, not a claim of success.

Baselines

The naive reference point is a single-task network for each of T, N and M, trained with plain cross-entropy on the observed pathological labels. This is the setting in which Wang et al. found lymph node prediction did not benefit from sharing.

The second baseline is plain multi-task training with a summed loss, matching the Wang et al. architecture of a two-layer, 64-unit shared trunk. Static loss weights are tuned per task on validation data with the same search budget given to every method.

The strongest existing competitor is conflict-avoidant multi-task optimization. We run MoDo as described in M2ASR, and we adapt ETR-NLP's split between shared and task-specific parameters to fully connected layers, sweeping its sharing ratio. These are the methods the file's own gap analysis would reach for. On their home benchmarks M2ASR reports a 38.6% average WER reduction on Librispeech and AISHELL, and ETR-NLP reports +3.56 mIoU on Cityscapes. Neither number transfers to staging. For conflict-avoidant multi-task staging on SEER there is no reported result found on Lacuna. The closest reported staging numbers come from different setups: an external SEER AUC of 79.3 for a random survival forest predicting survival (Yuan et al.), and 76% lymph node accuracy for the multi-task network on a private cohort (Wang et al.). Our own runs therefore establish the competitor's numbers, and every method gets the same features, splits, training budget and number of hyperparameter trials.

The key ablation adds the sampling-aware loss to plain multi-task training, both with and without MoDo. Beating the strongest baseline means two things. On held-out patients whose labels are trustworthy (18 or more examined nodes), the sampling-aware model must achieve higher nodal AUROC and better calibration than MoDo or ETR-NLP, with bootstrap intervals excluding zero. And MoDo layered on top of the sampling-aware loss must add no significant further gain. If MoDo still helps substantially, the interference is real and our "label noise" account is incomplete.

Why not just…?

Why not just drop patients with fewer than 18 examined nodes? This is the most serious threat. It is cheap and directly removes the noisy labels. It also discards a large fraction of patients, and it selects toward hospitals and procedures that dissect extensively, which is a population shift. We run it as a baseline under the same evaluation. If filtering matches the sampling-aware loss on high-node test patients and on the held-out registry sites, we will report that the simple fix suffices. The remaining contribution would then be the diagnostic finding about where interference comes from.

Why not just predict LODDS or the positive-node ratio instead of binary N? These measures were designed by Zou et al. and Fan et al. to be less dependent on how many nodes were examined, so regressing them is a plausible substitute target. The difficulty is that a zero-positive patient with three examined nodes and one with thirty still receive nearly opposite certainty under our model, but similar, deterministic targets under LODDS regression. We include LODDS regression as a nodal head and compare it on the same trusted-label evaluation.

Why not just use generic noisy-label methods such as label smoothing or small-loss sample selection? These methods do not know which labels are likely wrong. Our model has a per-patient covariate that says so. The semi-synthetic experiment below, where true labels are known, measures whether that knowledge matters. We run both generic methods at equal tuning budget.

Why not just train separate single-task models? Separate models remove interference by construction. Wang et al. report, however, that sharing improved three of four staging targets significantly. If single-task N with the sampling-aware loss equals multi-task N with it, sharing buys nothing for N, and we will say so.

Proposed Experiments

The decisive check is semi-synthetic and has ground truth. We take SEER patients with at least 18 examined nodes and treat their pathological N as true. We then simulate sparser dissections by subsampling examined nodes without replacement, so the observed positive count follows a hypergeometric draw from the recorded positive and examined counts. This produces corrupted training labels whose corruption rate depends on the simulated node count, exactly as stage migration would.

Under plain multi-task training, we measure the cosine similarity between the T-loss and N-loss gradients on the shared trunk, stratified by simulated node count. The prediction is that negative cosine, the operational sign of conflict, concentrates in low-count pN0 patients. It should largely vanish under the sampling-aware loss, and MoDo should recover much less of the true-label accuracy. We also check that the fitted detection curve tracks the curve actually used in the simulation.

On real SEER data, where true N is unobserved, the arbiter is survival. Among pN0 patients with few examined nodes, those the model flags as likely occult-positive should have survival closer to pN+ patients than to well-dissected pN0 patients. We measure this with hazard ratios and with the C-index of survival models that use predicted rather than recorded N.

The RADCURE arm reports whether the sampling-aware loss correctly yields no gain where no surgical sampling exists. It also reports how much interference remains in image-based multi-task staging when the conflict-avoidant baselines are run on the tumor-and-node graph features of Kazmierski and Haibe-Kains.

All results are additionally reported on held-out registry sites, to show whether the label correction survives the cross-center shift that the reproducibility literature identifies as the usual failure point.