The M1-to-M2 Switch as a Time-Varying Survival Covariate

When tissue is injured, immune cells called macrophages first take on an inflammatory state (labeled M1) that clears debris, and then switch to a healing state (M2) that rebuilds tissue. In diabetic wounds, heart attacks, and spinal cord injuries, this switch often arrives too late or not at all, and repair stalls. The biology literature measures this switch the way it measures almost everything: sacrifice some animals on day 3, more on day 7, more on day 14, and compare group averages. Meanwhile, survival analysis — the statistics of "time until an event happens," built to handle censored observations where the event hasn't occurred by the end of follow-up — has exactly the machinery this question wants: time-to-event outcomes, covariates that update over time, and a hazard, meaning the instantaneous rate of the event given everything known so far. But the field's workhorse, the Cox proportional hazards model, assumes each risk factor's effect is constant over time, and that assumption is precisely wrong here. Inflammatory macrophages are required and protective in the first days after injury and become destructive if they persist — a risk factor whose effect reverses sign over time.

This proposal builds and tests a survival model in which the macrophage polarization state is a latent, continuously valued variable that evolves over time and enters the hazard through a coefficient that is itself allowed to change sign. The model's central derived quantity is the crossover time: the day on which lingering M1 dominance stops being part of normal repair and starts predicting failure. Nothing in the supplied literature does this. The closest papers either predict a binary healed/not-healed label from polarization genes using penalized logistic regression (Adipose-Derived Mesenchymal Stem Cells Accelerate Diabetic Foot Ulcer Healing...), or run rigorous Cox models on the timing of an immune-modulating therapy without measuring macrophages at all (Delaying BCG immunotherapy onset...), or report Kaplan-Meier survival differences next to static polarization histology without ever connecting the two statistically (TRIM21 aggravates cardiac injury...).

Core Claim

The claim is that the timing and speed of the M1-to-M2 transition, not the level of polarization at any single time point, governs the hazard of repair failure — and that a time-dependent Cox model with a sign-reversing coefficient both captures this and yields a clinically useful biomarker, the estimated crossover time, that static snapshots cannot. Formally, let $z_i(t)$ be a continuous polarization score for subject $i$ at time $t$ (positive = M1-dominant, estimated from noisy marker panels rather than assumed binary), and let $w_i$ be fixed covariates including treatment arm. The model is

$$h_i(t) = h_0(t)\,\exp\!\big(\beta(t)\, z_i(t) + \psi^{\!\top} w_i\big), \qquad \beta(t) = \theta_1 - \theta_2 \,\sigma\!\big((t - \tau)/\sigma_t\big)$$

where $h_i(t)$ is the hazard of the event (wound closure failure, or death after cardiac injury), $h_0(t)$ is an unconstrained baseline hazard, $\sigma$ is a logistic function, and $\tau$ is the crossover time at which $\beta(t)$ changes sign. The parameters $\theta_1, \theta_2, \tau, \sigma_t, \psi$ are estimated by maximizing the time-dependent partial likelihood, with $z_i(t)$ obtained either by a two-stage route (smooth the observed marker trajectories, then fit) or jointly. The design is deliberately semi-parametric in time so that no one imposes where the crossover sits; the data locate it.

Three pieces of prior work motivate this design rather than merely inspiring it. First, the biological premise that M1 activity is beneficial early and pathological late is established across the wound and implant literature (Immune dysregulation and macrophage polarization in peri-implantitis, Innovative wound management...) — this is exactly the crossing-hazards regime that constant-coefficient models handle badly. Second, Deep Cox Mixtures showed that when survival curves cross, a standard Cox model can rank well while being badly miscalibrated, reporting an Expected Calibration Error of 0.0992 on the FLCHAIN dataset versus 0.0200 for their mixture model (Deep Cox Mixtures for Survival Regression); that paper buys non-proportionality through between-subject heterogeneity (latent groups with different baseline hazards), whereas our non-proportionality is within-subject and driven by an evolving, measurable biological state — a different mechanism requiring a different model. Third, tdCoxSNN proved that feeding longitudinal measurements into a time-dependent Cox neural network beats baseline-only prediction on real medical cohorts (Dynamic Prediction using Time-Dependent Cox Survival Neural Network), but its covariate coefficients are time-constant, so a marker whose effect flips sign remains outside its reach. Our proposal is that extension.

One honest scope note: the hazard ratio's causal meaning under time-varying covariates is contested, and On Defense of the Hazard Ratio defends its interpretability only under specific conditions, while unobserved heterogeneity and time-varying confounding (healing status itself feeds back into polarization) remain open. We therefore frame the model as predictive and descriptive — it locates the window and quantifies association within it — and reserve causal claims for the randomized treatment arms, where polarization is perturbed by design.

Research Program

The program has four connected parts. The first is the polarization score $z(t)$. The peri-implantitis review emphasizes that in-vivo macrophages exist on a continuum and no agreed marker panel separates intermediate states (Immune dysregulation and macrophage polarization in peri-implantitis), so we treat polarization as latent and estimate it from whatever markers a study measured — flow cytometry ratios (CD86/CD206), cytokines (TNF-$\alpha$, IL-10), or gene expression. To anchor the gene-expression route, we reuse the diabetic-foot-ulcer microarray pipeline from Cao et al., who condensed 631 polarization-related genes into differentially expressed macrophage markers across GSE134431 and GSE80178 and validated on GSE143735 (Adipose-Derived Mesenchymal Stem Cells Accelerate...); instead of thresholding into a two-gene classifier, we fit a one-dimensional score (a graded version of their screen) and check that it separates the same datasets their Firth model separated, with their external validation AUC of 0.944 as the reference point.

The second part is the estimation machinery: the time-dependent partial likelihood with $\beta(t)$ parameterized as above, plus a simpler competing specification using piecewise-constant $\beta$ over intervals, so that the sigmoid-versus-piecewise choice is itself testable rather than assumed. Where high-dimensional molecular covariates are available alongside the scalar score, structured variable selection with overlapping group penalties (Structured learning in time‐dependent Cox models) will select pathway-level features (for example the ABCA1/ABCG1 lipid-efflux axis highlighted in spinal cord injury work Rescuing macrophage normal function in spinal cord injury...) under strong heredity, since that paper showed plain Cox-LASSO selects noise and orphaned interactions.

The third part assembles evaluation data, because no public dataset with both longitudinal polarization measurements and time-to-event outcomes exists — we say this plainly, since it is both the gap and the burden. We will build three tiers. Tier one is a simulation benchmark whose parameters are calibrated to reported effect sizes from the file: the 54% versus 69% five-week survival gap between wild-type and TRIM21-knockout mice (TRIM21 aggravates cardiac injury...), the 14% M1 reduction and 181% M2 increase under adipose-stem-cell treatment (Adipose-Derived Mesenchymal Stem Cells...), and the timing sensitivity of immune therapy in the bladder-cancer cohort, where delaying BCG past a 101-day threshold raised recurrence hazard to 1.62 and progression hazard to 3.34 (Delaying BCG immunotherapy onset...). Tier two is a reanalysis of published in-vivo studies by digitizing their Kaplan-Meier curves to reconstruct pseudo-individual-level event times and pairing them with the polarization marker trajectories reported at fixed sacrifice points — arm-level, not individual-level, and we will label every conclusion from this tier accordingly. Tier three is a prospective murine diabetic-wound study (streptozotocin-induced, matching the Cao et al. design) with serial minimally-invasive wound-bed sampling for M1/M2 markers on days 0–21, the event defined as complete epithelialization, right-censoring at day 28, and randomized arms of vehicle versus an established immunomodulator drawn from the file's intervention set — the Alg-Mg/SF magnesium-releasing hydrogel (Innovative wound management...) or optogenetically loaded exosomes (Optogenetic engineered umbilical cord MSC-derived exosomes...) — sized so the crossover time is estimable with usable confidence intervals.

The fourth part turns $\hat{\tau}$ into a decision variable: using the recommender-function construction from DeepSurv (DeepSurv: personalized treatment recommender system...), which computes the difference in predicted log-risk between treatment options, we ask whether the model can identify when an intervention should be applied — specifically whether animals whose predicted crossover time falls before the intervention window benefit from delayed rather than immediate anti-inflammatory treatment, mirroring the ~100-day timing threshold the BCG study found in patients.

Baselines

The naive reference point is what the biology papers themselves do: Kaplan-Meier curves per treatment arm with a log-rank test, exactly as in the TRIM21 knockout study, which reported 54% versus 69% five-week survival with no hazard ratio or covariate adjustment (TRIM21 aggravates cardiac injury...). Beating this baseline means producing covariate-adjusted, time-resolved effect estimates with confidence intervals and subject-level risk predictions at multiple horizons — things a log-rank test cannot give at any budget. We will report it anyway, because if the prospective study's arms are so cleanly separated that nothing else matters, the added model has to justify itself elsewhere.

The strongest single-method competitor on discrimination is DeepSurv, a feed-forward neural network that replaces the Cox model's linear risk score with a learned nonlinear function and which reported a C-index of 0.867 on METABRIC versus 0.816 for the standard Cox model and 0.619 for a random survival forest (DeepSurv: personalized treatment recommender system...). We will run DeepSurv with all baseline information available at day 0 (initial marker panel, treatment arm, host covariates) and give it the same training folds, the same nested cross-validation tuning budget, and the same censoring pattern as our model. Beating it means higher landmark C-index at intermediate horizons (days 5, 10, 15) — horizons at which a baseline-only model is structurally blind — and lower calibration error. The threat is real and we will not hide it: on simulated data where the log-risk is linear in the covariates, the same paper shows standard Cox (C-index 0.779) matching DeepSurv (0.778), so the deep component only earns its keep under nonlinearity, and our ablations must show where that regime holds.

The strongest competitor on calibration is Deep Cox Mixtures, which reported FLCHAIN Expected Calibration Error of 0.0200 against the standard Cox model's 0.0992 precisely in a crossing-survival-curve setting (Deep Cox Mixtures for Survival Regression). It will receive the same features, including our estimated $z(t)$ trajectory, and the same tuning budget. Beating it means matching its calibration while additionally recovering the crossover time $\tau$, a quantity DCM does not define because its non-proportionality lives in mixture weights over baseline hazards rather than in a within-subject time-varying effect.

The key ablation isolates the one ingredient the proposal actually adds: the time-varying coefficient. We run our full model with $\beta(t)$ replaced by a constant $\beta$ — which reduces it to a time-dependent-covariate Cox model in the tdCoxSNN style (Dynamic Prediction using Time-Dependent Cox Survival Neural Network) — on identical data. A second ablation replaces the latent continuous score with the crude binary M1/M2 ratio actually reported in most studies, testing whether the latent-state machinery matters or a raw ratio suffices. If the constant-$\beta$ ablation matches the full model on C-index, calibration, and $\tau$-recovery, the proposal's central claim is wrong and we will say so.

Why not just…?

Why not just classify healed-versus-unhealed at day 21 with logistic regression? This is the established approach and it works: Cao et al. achieved an external-validation AUC of 0.944 with a two-gene Firth regression signature (Adipose-Derived Mesenchymal Stem Cells...). If the scientific question were "will this wound be healed on day 21, with no censoring," logistic regression would be the right tool and our model would be over-engineering. But the binary endpoint discards when healing occurred, cannot absorb censored animals (sacrifice, endpoint rules, drop-out) without bias, and cannot express the question this proposal exists to answer — when the M1 state turns from helpful to harmful, which the BCG timing study shows is where the actionable biology lives, with hazard ratios moving from 1.62 to 3.34 across delay windows (Delaying BCG immunotherapy onset...). Our decisive check is honest about the boundary: at the single day-21 horizon with no censoring, we expect a well-tuned logistic model to match our model, and we will report that parity; the differences should appear at earlier horizons, under censoring, and in the recovered crossover time.

Why not just use a standard Cox model with the M1/M2 ratio as a covariate? This is the most reasonable skeptical position, and the evidence against it is direct: when survival curves cross — which is exactly what a sign-reversing effect produces — the standard Cox model miscalibrates severely, with FLCHAIN calibration error of 0.0992 versus 0.0200 for a model that accommodates non-proportionality (Deep Cox Mixtures for Survival Regression). A constant-coefficient model forced onto a protective-early/harmful-late covariate will estimate something near a weighted average of two opposite effects, which is uninterpretable and hides the crossover. Our simulation study makes this quantitative: we will report the bias and coverage of the constant-$\beta$ estimate and the Schoenfeld-residual test's power to reject it, so if the constant model is actually adequate in the realistic-noise regime, the experiment will reveal that rather than our asserting it.

Why not just run Kaplan-Meier curves per group, as the TRIM21 study did? It requires no new methods and the field accepts it. But it is arm-level only: it cannot adjust for host covariates, cannot use the continuously measured polarization data the newer studies already collect, cannot produce subject-level predictions, and cannot express a crossover time at all. The TRIM21 paper's own data illustrate the cost — a 15-point survival difference with no mechanism linking it to the measured M1/M2 marker changes (TRIM21 aggravates cardiac injury...). Our KM-digitized reanalysis of that same study is precisely the experiment that shows what the extra machinery recovers on top of the log-rank test.

Why not just apply tdCoxSNN off the shelf? This is the closest existing method and the biggest threat, since it already handles longitudinal measurements in a time-dependent Cox framework and beat baseline-only prediction on the AREDS and PBC2 cohorts (Dynamic Prediction using Time-Dependent Cox Survival Neural Network). But its coefficients are constant in time, so it can consume a polarization trajectory yet still cannot represent the effect reversing sign; on our simulated sign-reversing data we expect it to inherit the Cox model's averaging pathology while paying the deep model's tuning cost. The constant-$\beta$ ablation above is exactly this comparison run fairly, and if tdCoxSNN matches the full model despite the misspecification, that result would itself be worth publishing — it would say the sign reversal is empirically negligible, contradicting the biological literature's central premise.

Proposed Experiments and Decisive Checks

The simulation benchmark comes first and carries the statistical weight: longitudinal marker trajectories with realistic noise, event times generated under sign-reversing $\beta(t)$ calibrated to the reported numbers above, and censoring patterns matched to a 21–28 day animal study. Success is defined in advance: the full model must recover $\tau$ with low bias and nominal confidence-interval coverage where the constant-$\beta$ model and Deep Cox Mixtures cannot define it, must beat the constant-$\beta$ ablation on landmark C-index and Expected Calibration Error, and must not lose to standard Cox when the true effect is time-constant (a falsification arm included deliberately, motivated by the linear-regime result where standard Cox matched DeepSurv at 0.779 versus 0.778 DeepSurv). The gene-expression polarization score is validated on the GEO diabetic-foot-ulcer datasets, with Cao et al.'s external-validation AUC of 0.944 on GSE143735 as the bar a continuous score should approach before being used downstream (Adipose-Derived Mesenchymal Stem Cells...); no reported result exists on Lacuna for survival outcomes on GSE134431 or GSE80178, so no survival comparison is possible there and none is claimed.

The KM-digitization reanalysis applies the model to reconstructed event times from the TRIM21 myocardial-infarction study, with the PCSK9 remodeling study supplying additional polarization trajectory calibration even though it contains no survival data at all (PCSK9 Modulates Macrophage Polarization-Mediated Ventricular Remodeling...); conclusions from this tier are arm-level and reported as such. The prospective wound study is the decisive biological check: pre-registered prediction that the estimated crossover time $\hat{\tau}$, computed from markers through day 5, stratifies time-to-closure better than any single-snapshot M1/M2 ratio, and that the treatment arm shifts $\hat{\tau}$ earlier in a dose-consistent way. The decisive negative results are equally pre-registered: if Schoenfeld-residual tests fail to reject proportionality on real marker data, if the constant-$\beta$ ablation matches the full model, or if the day-21 logistic baseline matches at every horizon, the central claim does not survive and the paper becomes a careful null result about a plausible but wrong model — which, given how strongly the biology literature asserts early-M1 benefit, would itself change how these experiments are analyzed.