Cell-State-Resolved, Time-Varying Hazards of NF-κB Signaling after Reperfusion Injury

When blood flow returns to an ischemic organ — after thrombectomy in stroke, revascularization in heart attack, or reperfusion of a transplanted kidney — the tissue suffers a second wave of damage driven by mitochondria that suddenly dump reactive oxygen species and by sterile inflammation. This ischemia-reperfusion injury (IRI) is now known to be a marathon, not a sprint: a single 21-minute ischemic insult in mouse kidney triggers a cascade that unfolds over 12 months, moving from an acute oxidative burst to attempted repair to chronic fibrosis and organ failure, with seven distinct temporal gene-expression modules along the way (Molecular characterization of the transition from acute to chronic kidney injury following ischemia/reperfusion). Meanwhile, the best-validated molecular risk marker in human transplants — a three-gene inflammatory macrophage signature that predicts graft failure 18 months before symptoms, with a hazard ratio of 3.24 (Inflammatory macrophage–associated 3-gene signature predicts subclinical allograft injury and graft survival) — comes from bulk tissue homogenates, so it cannot tell us which cells carry the risk or when that risk acts.

The core obstacle is that all three types of existing evidence are measured at the wrong resolution for the question. Bulk transcriptomics averages over millions of cells, blending parenchymal injury with infiltrating immune polarization into a single "smoothie" signal (Genome 2011). Clinical survival models on transplant registries rank risk well from hundreds of variables but contain no molecules at all. And mechanistic studies of the TLR4/MyD88/NF-κB to NLRP3-inflammasome axis — the pathway that primes pyroptotic inflammatory cell death after reperfusion — stop at 24-hour infarct volumes and cytokine blots, never asking how suppressing this pathway changes the rate of long-term organ failure (Ursolic acid ameliorates cerebral ischemia-reperfusion injury by inhibiting NF-κB/NLRP3-mediated microglia pyroptosis and neuroinflammation; C1q/TNF‑related protein 9 decreases cardiomyocyte hypoxia/reoxygenation‑induced inflammation by inhibiting the TLR4/MyD88/NF‑κB signaling pathway).

Core Claim

I propose to build and validate a cell-state landmark hazard model for post-reperfusion graft failure: deconvolve longitudinal bulk biopsy transcriptomes into cell-type proportions and cell-state-specific NF-κB/NLRP3 module scores, then fit a survival model whose regression coefficients are allowed to vary over follow-up time. The claim this would test is threefold. First, the hazard driven by NF-κB-pathway activity is concentrated in a small number of infiltrating myeloid states that bulk profiles conflate with parenchymal injury — so bulk signatures systematically misattribute the risk. Second, that hazard is strongly non-proportional, with an acute phase acting over days (consistent with NLRP3-mediated pyroptosis) and a separate chronic phase acting over years (consistent with indolent macrophage-driven fibrosis), which is exactly the pattern the constant-hazard-ratio assumption of the standard Cox model cannot represent (Deep Learning for Patient-Specific Kidney Graft Survival Analysis; FunCQNet: A Functional Censored Quantile Neural Network for Predicting Long-Term Post-Transplant Kidney Survival). Third, the fitted model supports a counterfactual analysis that predicts which cell type and which time window pharmacologic NF-κB inhibition should target to maximally reduce long-term graft-failure hazard — a quantitative, time-resolved answer that neither the acute preclinical studies nor the static bulk Cox analyses can give.

The model itself is a straightforward extension of established pieces rather than a new architecture: a Poisson birth-death bridge deconvolution that respects the integer-count geometry of RNA sequencing (Count Bridges enable Modeling and Deconvolving Transcriptomic Data), an ontology-aware embedding that keeps closely related myeloid sisters from being confused while anchoring deconvolution to a single-cell reference tree (Cross-modal transfer learning for mapping bulk transcriptomes at cellular level), and a landmark Cox formulation with piecewise-constant coefficients. Writing the cell-state covariates as $s_{ik}(t)$, the deconvolved abundance-and-module score for cell state $k$ in graft $i$ at landmark time $t$, the hazard is $h(t \mid s_i) = h_0(t)\exp\big(\sum_k \beta_k(t)\, s_{ik}(t)\big)$, where each $\beta_k(t)$ is estimated separately within a small number of follow-up windows (for example, 0–6 months, 6–24 months, beyond). The scientific payload is the shape of $\beta_k(t)$: if NF-κB-module activity in inflammatory macrophage states carries a large positive $\beta_k$ in the early window that decays, while a different state carries late-window risk, the non-proportionality is demonstrated and the intervention window is quantified.

Research Program

The program has three computational stages and one preclinical validation arm. The anchor dataset is the longitudinal kidney allograft protocol-biopsy cohort of 1,697 biopsies across 15 cohorts (kidney, heart, lung) with linked graft-survival outcomes used by the M1-signature paper, together with the prospectively timed 0-, 6-, and 24-month protocol biopsies of GSE25902 in which a 6-month biopsy predicts 24-month damage with 91.6% sensitivity and 83% specificity (Inflammatory macrophage–associated 3-gene signature predicts subclinical allograft injury and graft survival). Deconvolution will be trained against single-cell reference atlases in the spirit of POPPY's cross-attention querying, with the Cell Ontology's hierarchy penalizing confusion between biologically distant lineages; this matters because the reference may lack intermediate, damaged parenchymal states, a known bias of atlas-dependent methods (Cross-modal transfer learning for mapping bulk transcriptomes at cellular level).

Second, the landmark hazard model will be fit to graft-failure outcomes with three covariate families: cell-state proportions, cell-state-specific NF-κB/NLRP3 module scores (a curated set of TLR4/MyD88/RELA/NLRP3/CASP1/GSDMD targets plus the downstream cytokines), and standard clinical variables. The mouse data provide an independent dynamical check: the 10-timepoint, 2-hour-to-12-month bulk series of GSE98622 with its seven temporal modules (Molecular characterization of the transition from acute to chronic kidney injury following ischemia/reperfusion) lets us test whether the deconvolved myeloid NF-κB module peaks in the same acute module identified in mouse, and the 60.7% conservation between early mouse IRI genes and 1-hour human reperfusion biopsies (GSE43974) justifies carrying the mouse-learned time structure over as a prior, not just a sanity check.

Third, the counterfactual intervention analysis: holding all else fixed, clamp the myeloid NF-κB module score to its sham level in each follow-up window and recompute predicted survival. The output is a ranked table of cell-type-by-window interventions. This is calibrated against two pieces of in-file evidence — the ursolic acid study's demonstration that an NF-κB agonist (PMA) fully abolishes protection, proving continuous pathway suppression is required (Ursolic acid ameliorates cerebral ischemia-reperfusion injury by inhibiting NF-κB/NLRP3-mediated microglia pyroptosis and neuroinflammation), and the concern that blanket systemic inhibition risks immunosuppression and impaired parenchymal regeneration, since NF-κB plays pro-survival roles in some lineages. The preclinical arm tests the model's top-ranked and bottom-ranked interventions directly: a myeloid-restricted IKKβ deletion versus systemic NF-κB inhibition, in the 21-minute bilateral renal clamping protocol with 12-month longitudinal follow-up and the fibrosis/tubular-atrophy readouts of the established mouse model, scored against the model's predicted hazard trajectories.

Baselines

The "do nothing" reference point is current practice: surveillance biopsies interpreted with the existing three-gene M1 macrophage signature (CXCL11, CCL19, CD86), which reported a hazard ratio of 3.24 for graft failure corrected for time since transplant, a mean AUC of 0.91 across three independent renal transplant datasets, and the 6-month-to-24-month prediction at 91.6% sensitivity and 83% specificity (Inflammatory macrophage–associated 3-gene signature predicts subclinical allograft injury and graft survival). It is the strongest competitor because it is the only published method on these exact cohorts that links molecular measurements to graft survival; we will run it on identical cohort splits and evaluate with time-dependent concordance over the follow-up windows plus integrated Brier-score calibration, since a single static hazard ratio cannot express whether early or late prediction improves. Beating it means matching or exceeding its discrimination at every landmark while additionally returning per-cell-state, per-window hazard attribution it structurally cannot provide — if the time-dependent C-index improves only by a trivial margin, the mechanistic attribution alone should not be sold as predictive progress.

The strongest existing method at the right resolution is scSurv, the single-cell survival model that deconvolves bulk profiles into latent cell states and regresses them in an extended Cox model (scSurv: a deep generative model for single-cell survival analysis). It has never been applied outside oncology and COVID-19 cohorts; on Lacuna, no reported result is found for scSurv on transplant or ischemia-reperfusion data — its published result is a c-index above 0.5 across multiple TCGA cancer types, with no transplant-relevant number available. We will port it to our data unchanged except for inputs (same deconvolved cell-state features, same splits, same tuning budget by random search over matched hyperparameter counts) so the comparison isolates the two things scSurv lacks: count-aware deconvolution and time-varying coefficients.

Two ablations isolate the proposal's key ingredients. Fitting our own model with constant $\beta_k$ (collapsing the windows) isolates the non-proportional-hazards ingredient; if the time-varying version does not beat it on time-dependent concordance and window-wise calibration, the non-proportionality claim fails. Replacing the Poisson-bridge deconvolution with a continuous-latent deconvolution in the scSurv style isolates the count-geometry ingredient; Count Bridges already outperformed CIBERSORTx and MuSiC on proportion recovery and STDeconvolve on spatial spots (Count Bridges enable Modeling and Deconvolving Transcriptomic Data), but the honest question is whether that advantage survives once a survival head is attached.

Why not just…?

Why not just run standard Cox regression on bulk expression? This is the obvious simplification, and the M1-signature paper already did it, reporting the HR of 3.24. The in-file evidence says where it falls short: conventional Cox achieved a C-index of only 0.60–0.63 on the 3,117-recipient Korean multicenter cohort while a survival-aware learner reached 0.80 (A Machine Learning Approach Using Survival Statistics to Predict Graft Survival in Kidney Transplant Recipients: A Multicenter Cohort Study), and linear Cox models cannot express the time-varying structure that the SRTR study explicitly flags as unrealistic in graft longevity (Deep Learning for Patient-Specific Kidney Graft Survival Analysis). More fundamentally, the M1 authors themselves could not tell whether their genes reflect infiltrating monocytes, resident macrophage expansion, or secondary parenchymal signaling — exactly the question our deconvolution answers. The decisive check is the constant-$\beta$ ablation run on identical bulk inputs: if bulk Cox matches our model's window-wise prediction, the heterogeneity-masking claim is wrong and I would report it.

Why not just use classical deconvolution (CIBERSORTx, MuSiC) plus a standard survival model? This is the cheapest pipeline and a real threat to the fancier generative components. The count-geometry argument is empirical, not aesthetic: Count Bridges beat both methods on bulk proportion recovery and outperformed STDeconvolve on spatial data (Count Bridges enable Modeling and Deconvolving Transcriptomic Data), and ontology-blind deconvolution is precisely what confuses sister myeloid states — the distinction our whole hypothesis rests on. The CIBERSORTx-plus-static-Cox pipeline will be run as an explicit additional baseline under the same budget; the count-bridge and ontology ablations are what settle whether the delta comes from the deconvolution or from the time-varying hazards, and if the classical pipeline matches within confidence intervals, the honest conclusion is that the time-varying hazard component is the paper and the deconvolution upgrade is not.

Why not just use clinical biomarkers like creatinine and eGFR? Because they are lagging indicators: the M1 signature detected progressive subclinical injury 18 months before clinical manifestation, and FunCQNet showed that even rich eGFR-trajectory models leave mechanism invisible — a rising creatinine cannot tell you whether to inhibit NF-κB in macrophages or protect it in tubular epithelium (FunCQNet: A Functional Censored Quantile Neural Network for Predicting Long-Term Post-Transplant Kidney Survival). The strongest registry model, the multi-task deep network on 131,709 SRTR transplants, reached a C-index of 0.6550 versus 0.6504 for Cox Efron (Deep Learning for Patient-Specific Kidney Graft Survival Analysis) — respectable ranking, zero mechanism. We will still fuse our cell-state features with the clinical variables, so the relevant comparison is whether molecular features add window-wise discrimination on top of the best clinical model, which is precisely what our evaluation reports.

Why not just use a Random Survival Forest for the non-linearity? Because trees cannot be trained jointly with the generative deconvolution encoder, and empirically they lag badly: on METABRIC, DeepSurv reached a C-index of 0.867 against 0.619 for the RSF (DeepSurv: personalized treatment recommender system using a Cox proportional hazards deep neural network). More to the point, RSF gives variable-importance scores, not per-cell-type, per-window hazard coefficients, so it cannot answer the counterfactual intervention question that motivates the work. We will include it as a secondary baseline on the same features anyway, since the cost is small.

Proposed Experiments and Decisive Checks

Experiment one is the retrospective human test on the 15-cohort biopsy collection and GSE25902: nested cross-validation across cohorts, evaluating window-wise time-dependent C-index, integrated Brier score, and the sign test on whether the myeloid NF-κB module's $\beta_k$ is significantly larger in the early window and decays. The pre-registered success criterion is beating the M1 signature's landmark-window discrimination while showing non-proportional coefficients with non-overlapping confidence intervals across windows; a null result where all $\beta_k(t)$ are flat would itself be informative, contradicting the biphasic expectation from the mouse modules. Experiment two is the mouse dynamical check on GSE98622 and the human cross-species check on GSE43974: the deconvolved myeloid NF-κB module must peak within the acute mouse module (2–24 hours) and its human ortholog must track early reperfusion response genes, otherwise the module definition is wrong. Experiment three is the counterfactual ranking plus the preclinical arm: myeloid-restricted versus systemic NF-κB inhibition in the renal clamping model, with the decisive readout being whether the model's top-ranked intervention reduces 12-month fibrosis and Krt20/Havcr1-tracked chronic markers more than the model's bottom-ranked one at matched pathway suppression. If systemic inhibition matches the targeted prediction, the cell-state-specificity hypothesis fails and the model should be re-centered on timing alone.