Time-Aware Alignment of Cytokine Rebalancing with Tissue Morphometry

Therapies that rebalance cytokines — dialing down pro-inflammatory signals like TNF-α and IL-6 while turning up protective ones like IL-10 and IL-22, rather than blankly suppressing the immune system — are typically judged by two very different measurements. One is a blood or homogenate assay: cheap, repeatable, and therefore longitudinal. The other is histopathology: a stained tissue section that shows whether the mucosa, crypts, and extracellular matrix were actually rebuilt, but which destroys the specimen, so it can only be taken once, at the end. Because these two measurements can never be taken on the same biological unit at the same time, studies of cytokine rebalancing treat them as separate endpoints and simply assert their connection. Worse, when such studies are run against historical controls — animals or patients treated in earlier calendar periods — both measurements inherit temporal confounding: drift in animal husbandry, staining protocols, scanners, and background care that masquerades as a treatment effect.

The opportunity is that a general recipe now exists for exactly the first half of this problem: Propensity Score Alignment of Unpaired Multimodal Data aligns two modalities that can never be co-measured (it was built for microscopy images and single-cell RNA sequencing, where the sequencing step destroys the very cell that was imaged) by training a per-modality classifier to predict the perturbation, then using the predicted probabilities as a shared coordinate and optimal transport to match samples across modalities. What that method does not handle is time: it assumed static, discrete genetic perturbations in vitro, with no calendar drift, no continuous exposure, and no in vivo tissue architecture. This proposal extends propensity alignment into a time-aware estimator that links a continuous cytokine-rebalancing state to quantitative tissue morphometry across non-concurrent cohorts, and validates it where the histology-ground-truth and era structure already exist.

Core Claim

When a rebalancing therapy is compared against historical controls using terminal tissue assays, the naive estimated effect on tissue structure is biased by calendar-time drift, and a cross-modal alignment whose propensity model carries calendar time explicitly — a time-aware propensity alignment — recovers an estimate indistinguishable from a concurrent randomized experiment, at a fraction of the animal cost. The claim has three parts, each falsifiable on existing benchmarks: that naive historical-control pooling produces spurious morphometric effects of the same kind that Randomized Clinical Trials or Convenient Controls: TREWS or FALSE? demonstrated clinically (a purely random "alert" produced an unadjusted spurious mortality difference of 3.3% versus 6.4% in a 231,441-encounter cohort, $p < 0.001$, erased only by explicit process-of-care adjustment); that static baseline propensity matching, as used in the Qingchang Yuyang decoction ulcerative colitis study, cannot remove this bias; and that adding calendar time and a continuous rebalancing exposure to the propensity alignment removes it.

The cytokine side is modeled not as a binary treated/untreated flag but as a continuous rebalancing index, for example

$$R_i = \log \frac{[\text{IL-10}]_i + [\text{IL-22}]_i}{[\text{TNF-}\alpha]_i + [\text{IL-6}]_i + [\text{IL-1}\beta]_i},$$

measured per subject over time from the cheap longitudinal assay. This choice is forced by the evidence: in the Emory ALS registry, binary propensity analysis of gastrostomy insertion found no benefit (an effect of $-0.17$ on BMI), while modeling the continuous timing of insertion via generalized propensity scores revealed a significant positive effect of 2.69 (95% credible interval 0.82 to 4.53), showing that collapsing a time-varying exposure into a flag can flip the sign of a real effect (Estimating the palliative effect of percutaneous endoscopic gastrostomy in an observational registry using principal stratification and generalized propensity scores). The histology side is a quantitative morphometric vector — villus height, crypt depth, their ratio, goblet-cell counts per villus, collagen fraction by Masson's trichrome — the indices already standard in the TNBS rat colitis repository (Bacteroides fragilis capsular polysaccharide A ameliorates ulcerative colitis in rat by recovering intestinal barrier integrity and restoring gut microbiota) and in aquaculture morphometry (Effect of Dietary Supplementation of Glycerol Monolaurate on Growth Performance, Digestive Enzymes, Serum Immune and Antioxidant Parameters, and Intestinal Morphology in Black Sea Bream).

Research Program

The built artifact is an estimator with three components. First, a generalized propensity score $e(t_i, R_i, \mathbf{x}_i)$ gives the probability that subject $i$, with covariates $\mathbf{x}_i$ and observed rebalancing trajectory, belongs to harvest era $t_i$; this extends the ALS-paper construction from a scalar insertion time to (era, dose) jointly, and supplies the shared low-dimensional coordinate that made the original propensity alignment work. Second, entropic optimal transport matches cytokine-side subjects to histology-side slides, with a transport cost that penalizes era mismatch:

$$c(i, j) = |e_i - e_j|^2 + \lambda\, d(t_i, t_j) + \gamma\, \|\mathbf{m}_j - \hat{\mathbf{m}}(R_i)\|^2,$$

where $\mathbf{m}_j$ is the morphometric vector of slide $j$, $\hat{\mathbf{m}}(R_i)$ is a regression of morphometry on the rebalancing index learned within overlapping eras, and $d(t_i, t_j)$ is calendar-time distance. The $\lambda$ term is the proposal's key ingredient: it prevents the transport from matching a modern treated animal to a decade-old control, which is precisely the historical-control failure. Third, model and hyperparameter selection use the R-risk of How to select predictive models for decision-making or causal inference, which reweights prediction error using nuisance propensity and outcome models and selected models within about 1% of oracle causal risk on Caussim/ACIC/Twins, versus roughly 10% excess risk for plain mean-squared-error selection; we adapt it to score candidate morphometry regressions whose inputs are high-dimensional histology embeddings, which that paper never evaluated.

For the histology encoder we use domain-specific models, not general ones: Foundation Models for Histopathology—Fanfare or Flair showed KimiaNet and DinoSSLPath consistently beat general vision-language models on retrieval and classification (DinoSSLPath reached 99.34% on DigestPath signet-ring-cell classification, while DinoV2 and CLIP derivatives lagged), so slide features come from KimiaNet-style encoders (75% on CAMELYON16 image-level search in that same evaluation).

The data program assembles a multi-era rat TNBS colitis archive: the published TP2 batches (Bacteroides fragilis capsular polysaccharide A..., whose 16S data are deposited under NCBI BioProject PRJNA1189676) supply the paired cytokine-plus-histology template; the archive is extended by aggregating contemporaneous and earlier TNBS/colitis batches with vehicle and prednisolone controls run at different calendar times, each with H&E/PAS slides re-scored by the same automated morphometry pipeline. A single newly run concurrent batch — induced, randomized, and sacrificed within one window, exactly as the TP2 study did — serves as held-out ground truth. In parallel, the method is exercised on the two large public histology archives whose era structure is documented but unmodeled: CAMELYON, 1,399 lymph-node slides from five centers over 2006–2016 (1399 H&E-stained sentinel lymph node sections of breast cancer patients: the CAMELYON dataset), and the 9,048-patient ten-cohort colorectal collection (Transformer-based biomarker prediction from colorectal cancer histology: A large-scale multicentric study).

Proposed Experiments

The synthetic experiment comes first: a Caussim-style simulator with an injected calendar-era drift and a destructive-assay split, where the true effect of the rebalancing index on morphometry is known. We measure the bias of the naive historical-control estimate, the static-PSM estimate, the original propensity alignment, and the time-aware version; the R-risk versus plain MSE comparison for selecting among candidate morphometry models is run on the same simulator, extending the R-risk evaluation beyond its original tabular benchmarks (How to select predictive models...). The second experiment injects artificial era labels into the CITE-seq benchmark used by Propensity Score Alignment of Unpaired Multimodal Data and asks whether time-aware transport maintains the alignment advantage that PS+OT showed over VAEs, SCOT, and scGLUE on mean-squared error and FOSCTTM (no reported result found on Lacuna for absolute MSE or FOSCTTM values on that benchmark, so we re-implement PS+OT and reproduce its qualitative ranking before injecting drift). The third experiment reanalyzes the era structure of the public archives: on CAMELYON, we test whether adjusting for acquisition year changes the estimated center and era effects that current pipelines absorb silently as visual noise, using the documented inter-scanner and protocol variation; on the colorectal cohorts, we compare era-adjusted biomarker prediction against the transformer baseline of Transformer-based biomarker prediction..., which reported MSI prediction with sensitivity 0.97 and negative predictive value 0.99 on surgical resections, an AUROC of 0.91 on external endoscopic biopsies, and cross-cohort variation of at most 0.08 AUROC. The fourth experiment is the decisive in vivo test on the multi-era rat archive: estimate the effect of rebalancing (TP2 and prednisolone arms versus historical vehicle controls) on each morphometric index, then compare against the held-out concurrent batch. The method passes if its confidence intervals cover the concurrent estimate while the naive historical-control estimate does not. A fifth, clinical-scope reanalysis applies the same estimator to the QCYD ulcerative colitis cohort (Effect of Qingchang Yuyang decoction on treatment efficacy and intestinal flora in patients with ulcerative colitis), which spanned June 2022 to June 2024 but matched only on static baseline covariates; we test whether its reported cytokine differences (higher IL-10, lower TNF-α and IL-8, $p < 0.05$; complication rate 14.00% versus 32.61%, $p = 0.030$) survive explicit temporal adjustment — noting honestly that this cohort has no biopsy morphometry, so it probes only the temporal component.

Baselines

The do-nothing reference is the naive pooled historical-control comparison: simply aggregate treated animals from recent batches with vehicle controls from earlier batches and compute mean morphometric differences. This is the default practice the field would fall back to, and the TREWS study gives a calibrated expectation of how badly it fails — a purely random assignment produced an unadjusted mortality difference of 3.3% versus 6.4% across 231,441 encounters (Randomized Clinical Trials or Convenient Controls: TREWS or FALSE?), so any pipeline that cannot null out a random pseudo-treatment across eras is disqualified on its face.

The strongest existing competitor is the original Propensity Score Alignment pipeline of Propensity Score Alignment of Unpaired Multimodal Data: per-modality treatment classifiers, propensity-probability shared coordinates, entropic optimal transport. On the CITE-seq benchmark it significantly outperformed multimodal VAEs, SCOT, and scGLUE on mean-squared error and FOSCTTM, and it generalized to unseen perturbations on the HUVEC Perturb-seq/microscopy task; no reported result found on Lacuna for its absolute metric values, so the comparison protocol is: same morphometric targets, same encoder, same era splits, same hyperparameter search budget, with its cost function left era-blind versus ours carrying era. Beating it means lower alignment error on drift-injected benchmarks and, more importantly, lower bias in the estimated rebalancing-to-morphometry effect on the simulator, since alignment error is only a proxy for the causal quantity we actually care about. For the pathology-prediction side experiment, the strongest baseline is the CTransPath transformer of Transformer-based biomarker prediction..., which reported MSI AUROC 0.91 on biopsies and sensitivity 0.97 with NPV 0.99 on resections; we run our era-adjusted variant on the identical cohort split with the same training budget.

An intermediate baseline is static propensity score matching on baseline covariates without any temporal terms — exactly what the QCYD study did — run on the same archive with the same covariate set. Finally, the ablation that isolates the key ingredient removes the era term $\lambda$ from the transport cost, which reduces our method to vanilla PSA, and separately removes optimal transport altogether, leaving only generalized-propensity stratification in the style of the ALS analysis; the gap between these ablations and the full method is the direct measurement of what temporal alignment buys.

Why not just…?

Why not just run a fresh concurrent randomized experiment? For the specific question "does TP2 rebuild tissue," yes — and our held-out concurrent batch is exactly that. But the scientific target is different: the archives. CAMELYON spans 2006–2016 and the colorectal cohorts span decades of acquisition; no prospective experiment can retroactively create era variation or evaluate long-elapsed structural adaptation, and Generating the right evidence at the right time: Principles of a new class of flexible augmented clinical trial designs argues that even prospective concurrent designs pay for internal validity with external validity and access delays. The honest residual risk is cost-benefit: if concurrent experiments are always affordable, the historical archive is redundant. Our response is empirical — quantify how much era drift actually exists in the rat archive; if the naive and concurrent estimates already agree, temporal correction is unnecessary there, and the value of the method rests on the public archives, where ten-year scanner and protocol drift is documented as real.

Why not just use baseline propensity score matching, as the QCYD study did? Three cited results say this falls short precisely at our intersection. The ALS registry analysis showed binary, time-blind propensity matching can return $-0.17$ where the time-aware generalized version returns 2.69 (Estimating the palliative effect of percutaneous endoscopic gastrostomy...); the TREWS coin-flip showed unadjusted (and workflow-unadjusted) comparison fabricates a highly significant effect from nothing; and the Variational Temporal Deconfounder showed that methods assuming all confounders are observed, like the G-formula, carry higher RMSE and IF-PEHE than latent-proxy deconfounding on longitudinal data with hidden confounders (Variational Temporal Deconfounder for Individualized Treatment Effect Estimation from Longitudinal Observational Data). That same VTD paper also cautions us: on some MIMIC-III tasks a method assuming unconfoundedness performed competitively, so the severity of latent temporal confounding is data-dependent — which is exactly why our design includes an era-drift quantification step before any correction is claimed necessary.

Why not just align the two modalities with a multimodal variational autoencoder? This is the natural deep-learning instinct, and it has already been tested and beaten: the propensity-alignment paper evaluated VAE-based methods on unpaired biological data and found they get "bogged down trying to model this irrelevant noise instead of focusing on the shared biological signal," with PS+OT significantly outperforming them on both MSE and FOSCTTM, and PS+OT's cross-modal predictions sometimes beating models trained on true pairs (Propensity Score Alignment of Unpaired Multimodal Data). Our proposal keeps the winning propensity-plus-transport skeleton and changes only what that work left open: the exposure becomes a continuous rebalancing index instead of discrete knockouts, the samples become in vivo tissue slides instead of cultured cells, and calendar era enters the matching objective. A VAE could still win if the shared biological signal were high-dimensional and rich; the drift-injected CITE-seq experiment is designed to settle that directly rather than by analogy.

Decisive Checks

Three checks decide the proposal. The negative control first: assign pseudo-treatment purely at random across eras in the rat archive, in the spirit of the TREWS coin-flip protocol; the time-aware estimator must return a null effect on every morphometric index, while we expect the naive pooled comparison to show spurious differences. Second, the recovery test: the estimated effect of rebalancing on morphometry from historical controls must fall within the confidence interval of the held-out concurrent batch — pre-registered indices, pre-specified tolerance. Third, the overlap stress test: the R-risk work showed causal model selection degrades sharply when population overlap between cohorts is poor, so we evaluate the estimator across a controlled range of era overlap in the simulator and report at what overlap it breaks; a method that only works when eras barely drift is not worth building, and we will say so. If all three pass, the practical payoff is concrete: every terminal-assay toxicity and efficacy study that already sits in a freezer or a scanner archive becomes admissible evidence about whether rebalancing cytokines actually rebuilds tissue, without a single additional animal.