Diabetic foot ulcers are open wounds that stall in a chronically inflamed, poorly vascularized state, and they are a leading route to amputation. Nearly every study of a new wound therapy declares success at a single early moment. Mouse studies stop at day 14 to 20. Clinical case series count a wound as healed one month after treatment. Hospital cohorts record only what happens before discharge. Yet the biology of these wounds suggests that closure can be fragile. High glucose drives skin and blood-vessel cells into premature senescence, a permanent arrest of cell division. Fibroblasts begin secreting vesicles that suppress new blood-vessel growth. Neutrophils overproduce extracellular traps, sticky webs of DNA that keep the wound inflamed. All of these could survive the moment the skin closes over. If so, a therapy that closes wounds faster could still leave patients with fewer ulcer-free days a year or two later.
This proposal asks a methodological question that has a direct clinical consequence: how often, and by how much, does truncating follow-up change the conclusion of a diabetic wound therapy comparison? We would treat the wound as a patient moving through states: open ulcer, healed, recurred, amputated, dead. We would estimate treatment effects on the expected time spent healed, using retrospective health-record cohorts with multi-year follow-up. Then we would deliberately re-analyze the same cohort as if it had been observed for only one month, three months, or the index hospitalization. The deliverable is a horizon-sensitivity curve. It shows how much of a therapy's apparent benefit survives as the observation window lengthens, and whether early benefit ever flips sign once recurrence and post-discharge amputation are counted.
Core Claim
The claim has three parts. First, binary "closure by time T" is the wrong endpoint for diabetic wounds. Second, a multistate estimand is computable from routine retrospective records and can be adjusted for confounding by indication. That estimand is expected ulcer-free time up to a horizon, with death treated as a competing outcome rather than ordinary censoring. Third, short-horizon analyses of the same cohort will systematically overstate, and sometimes reverse, the benefit of closure-promoting therapies.
Concretely, for horizon $\tau$, define the restricted mean ulcer-free time as
$$ \mathrm{RMUT}_a(\tau) = \mathbb{E}\left[\int_0^{\tau} \mathbf{1}\{S_a(t) = \text{healed}\}\,dt\right], $$
where $S_a(t)$ is the patient's state at time $t$ since ulcer presentation under treatment $a$. The quantity of interest is the curve $\Delta(\tau) = \mathrm{RMUT}_1(\tau) - \mathrm{RMUT}_0(\tau)$ traced over $\tau$ from one month to three years. The mechanistic hypothesis predicts a specific shape for this curve. A therapy that accelerates closure without repairing the senescent or inflamed wound bed should show a large early $\Delta$ that flattens or declines. The reason is that its patients spend more time in the healed state but leave it faster.
What is new is not survival analysis of diabetic foot ulcers as such. What is new is using the horizon itself as the experimental variable within a single confounding-adjusted cohort, so that the "sustainability gap" becomes a measured quantity instead of a disclaimer in a limitations paragraph.
Grounding in Prior Work
The motivating evidence comes from three places. The preclinical studies close wounds almost completely by two weeks. MiR‐17‐5p‐engineered sEVs report 97.24% closure at day 15 by relieving p21/PTEN-driven senescence. FGF21-engineered ADSCs report near-complete closure by day 14 by suppressing ferroptosis, an iron-dependent form of cell death. Neither study can say anything about durability. The mechanistic papers supply the reason durability might fail. Bian et al. show that high-glucose fibroblast vesicles actively suppress angiogenesis. Liang et al. show that ulcer tissue loses reparative fibroblasts and T and NK cells while neutrophil-trap genes rise. These are persistent tissue states, not acute ones. We use this biology only to generate the directional hypothesis about the shape of $\Delta(\tau)$; we do not measure it.
The closest clinical work shows the gap directly. Bruyeres et al. studied 28 chronic-wound patients treated with epidermal grafts. They assessed healing one month after the last graft (4 of 15 healed), with no control group and no recurrence tracking. Yuan et al. compared diabetic foot inpatients in Tibet and Beijing using unadjusted tests. They found that Tibetan patients had worse glycemic control (HbA1c 10.2% vs 8.7%) yet a lower in-hospital amputation rate (9.3% vs 29.8%). Both studies stop at the point where our analysis begins. The Tibet "paradox" is a natural test case: an in-hospital endpoint could plausibly produce it as an artifact if later amputations happen after discharge.
The methods come from the retrospective-cohort and dynamic-survival literature. Propensity adjustment for treatment-by-indication follows the logic of Tewari et al.. Chatha et al. embed a time-varying survival model in augmented inverse propensity weighting (AIPW), an estimator that combines an outcome model and a treatment-assignment model and stays consistent if either is right. They use it to target restricted mean survival time, and they validate on semi-synthetic outcomes built from real records. We reuse both the estimator and the semi-synthetic validation strategy, extending the target from a single death time to multistate ulcer-free time. Two papers act as constraints rather than templates. DySurv reports training instability and hyperparameter sensitivity in a deep survival model. Reply: Time‐Related Biases warns that immortal-time bias haunts cohort studies in diabetes. Our design therefore anchors time zero at ulcer presentation, assigns treatment within a fixed grace window, and does not depend on deep models for its main estimate.
Research Program
Cohort assembly. We would assemble a retrospective cohort from a health system whose records follow patients across inpatient, outpatient wound-clinic, and death-registry data for at least three years. The file supplies no public longitudinal diabetic foot cohort, so this is a data-access commitment, not an existing benchmark. Each patient's timeline is coded into five states. The state "healed" means documented complete epithelialization. Recurrence means a new or reopened ulcer at the same or another foot site, with the two analyzed separately. Major amputation and death are both absorbing states, meaning patients do not leave them. Wound area from clinic photographs, where available, can be extracted with segmentation models of the kind evaluated on FUSeg (Kuo et al.). These areas would serve only as time-varying covariates, not as endpoints.
Treatment contrast. The primary contrast is an advanced closure-promoting therapy, such as skin grafting or bioengineered dressings, versus standard offloading and debridement. It is specified as a target-trial emulation: the analysis copies the design of a hypothetical randomized trial, starting the clock at presentation and assigning treatment within a 30-day grace window. Covariates include age, diabetes duration, HbA1c, renal function, white-cell and neutrophil counts, ulcer grade, ischemia and infection status, and prior ulcers. These are the routine markers that the cohort papers in the file found informative.
Estimation. Transition hazards between states are estimated with a multistate model, both a parametric version and a flexible version, and combined with a propensity model in an AIPW estimator for $\Delta(\tau)$. Each estimate comes with a bootstrap confidence band across the full range of $\tau$.
Truncation emulation. The same cohort is then re-analyzed under the three designs used in the literature. The first is closure at one month after treatment, mimicking Bruyeres. The second is amputation during the index admission, mimicking Yuan. The third is closure at 12 weeks, the common clinical surrogate. Each truncated estimate is compared with the long-horizon $\Delta(\tau)$.
Baselines
The naive reference. This is the unadjusted, single-horizon analysis that dominates the field: the proportion healed at one month (or in-hospital amputation rate), compared between treatment groups with a chi-square test, as done by Yuan et al. and descriptively by Bruyeres et al.. It runs on the identical cohort with no tuning. It is the status quo that our horizon curves are meant to audit.
The strongest conventional competitor. This is a propensity-matched Cox model for time to first recurrence among healed patients, in the style of Tewari et al., using the same covariate set and caliper. It is the analysis a careful epidemiologist would run first, and it could plausibly capture much of what we claim. It shares our propensity model, so any difference comes from the estimand, not from adjustment.
The strongest modern method. This is the AIPW-with-dynamic-survival approach of Chatha et al.. Its reported result is a survival-time mean absolute error of 11.19, versus 16.04 for an oracle Cox model and 11.42 for a static transformer, on semi-synthetic MIMIC-III outcomes. We run it on our cohort targeting time to first amputation-or-death, under the same compute and hyperparameter search budget as our flexible multistate model. DySurv reports a C-index of 57.9 and integrated Brier score of 0.122 on MIMIC-IV. It is included only as a dynamic risk predictor for comparing calibration, since it does not estimate treatment effects. For any diabetic-ulcer recurrence task, no reported result was found on Lacuna, so all baselines will be measured fresh.
Ablations. Two ablations isolate the key ingredients. The first keeps full causal adjustment but swaps our estimand for binary closure at $\tau$; this tests whether the multistate structure matters. The second keeps the multistate estimand but treats death as ordinary censoring; this tests whether handling death as a competing outcome matters.
What counts as beating the baselines. In semi-synthetic data, our estimator must recover the true $\Delta(\tau)$ curve with lower bias and nominal confidence-band coverage, where the baselines' single-number summaries cannot. In real data, our estimand must reveal a horizon-dependent effect, meaning attenuation or sign change, that the matched recurrence Cox model misses or misstates.
Why not just…?
Why not just run a propensity-matched Cox model on time to recurrence? This is the real threat, and we take it seriously. If treatment affects only recurrence and not time to closure or death, the Cox hazard ratio and our $\Delta(\tau)$ will tell the same story, and the multistate machinery adds little. However, recurrence analyses condition on having healed, and healing is itself affected by treatment. Comparing only healed patients therefore compares non-comparable groups. Ignoring death as a competing outcome compounds this in a population with high mortality. Our first ablation tests this directly on the same data. If binary or recurrence-only analyses reproduce the full curve within its confidence band, we will report that the simpler analysis suffices, and the contribution narrows to the truncation audit.
Why not just use a deep dynamic survival model like DynST or DySurv? Those models were built and validated on tens of thousands of ICU stays, and they target a single event time. Diabetic foot cohorts will be one to two orders of magnitude smaller. DySurv already reports instability even at scale. We include DynST as a baseline. We expect its flexible outcome model to help only as the nuisance component inside AIPW, not as a replacement for the estimand.
Why not just accept 12-week closure as a validated surrogate? Whether 12-week closure tracks long-term outcomes is precisely what the truncation emulation measures. The file already gives reasons for doubt. Short windows miss late recurrence in other diseases (Yang et al.). The glycemic surrogate in Yuan et al. runs opposite to the hard outcome. If the surrogate's treatment ranking matches the three-year ranking, that is a useful positive finding we would publish as such.
Why not just run a randomized trial? A trial would be definitive for one therapy, but multi-year recurrence trials are slow and expensive. Such trials also tend to exclude the multimorbid patients who dominate diabetic foot care, the limitation the file attributes to RCTs generally (Chen et al.). Our horizon curves would tell trialists what follow-up length is actually needed.
Proposed Experiments and Decisive Checks
Semi-synthetic validation. Following Chatha et al., we keep the real covariates and simulate treatment assignment and state transitions under known scenarios. In scenario one, therapy speeds closure and has no effect on recurrence. In scenario two, therapy speeds closure and raises recurrence hazard. In scenario three, therapy affects only mortality. Metrics are bias, root-mean-square error, and band coverage of $\Delta(\tau)$ across horizons. The decisive check is scenario two. The one-month binary analysis should report a clear benefit, while the true three-year $\Delta$ is near zero or negative. Our estimator must recover the truth where the baselines cannot.
Real-cohort horizon curves. We estimate $\Delta(\tau)$ for the primary therapy contrast on the real cohort. We report the ratio of the three-year effect to the one-month effect and the horizon at which the confidence band first includes zero. The mechanistic hypothesis is falsified if closure-promoting therapies show undiminished or growing benefit with horizon.
The Tibet paradox, in miniature. Within whatever geographic or rural–urban variation the cohort contains, we compare in-hospital amputation contrasts with three-year amputation-or-death contrasts between groups. The question is whether a short-window advantage like Yuan's persists once post-discharge events are counted.
Sensitivity analyses. Residual unmeasured confounding is bounded with E-values, which report how strongly an unmeasured confounder would have to be associated with both treatment and outcome to explain away the estimate. Immortal-time bias is probed by varying the treatment grace window. A negative-control outcome, such as an unrelated hospitalization, checks for systematic bias in the adjustment.
References
- MiR‐17‐5p‐engineered sEVs Encapsulated in GelMA Hydrogel Facilitated Diabetic Wound Healing by Targeting PTEN and p21
- FGF21-engineered ADSCs promote diabetic wound healing by mitigating ferroptosis and oxidative stress via the SIRT1/NRF2/GPX4 signaling pathway
- Extracellular vesicles derived from fibroblasts induced with or without high glucose exert opposite effects on wound healing and angiogenesis
- Neutrophil Extracellular Trap-Related Genes and Immune Infiltration in Diabetic Foot Ulcers by Bioinformatics Analysis and Experimental Verification
- Efficiency of Epidermal Grafts in Chronic Wounds: A Retrospective Observational Study
- Clinical characteristics and the prognosis of diabetic foot in Tibet: A single center, retrospective study
- Long-Term Survival in Men With High Grade Prostate Cancer: A Comparison Between Conservative Treatment, Radiation Therapy and Radical Prostatectomy—A Propensity Scoring Approach
- Dynamic Survival Transformers for Causal Inference with Electronic Health Records
- DySurv: Dynamic Deep Learning Model for Survival Prediction in the ICU
- Reply: Time‐Related Biases in Observational Studies of <scp>GLP</scp> ‐1 Agonists and Cancer Risk
- Improving Limited Supervised Foot Ulcer Segmentation Using Cross-Domain Augmentation Strategies
- A predictive model using left atrial function and B‐type natriuretic peptide level in predicting the recurrence of early persistent atrial fibrillation after radiofrequency ablation
- Practice patterns and outcomes for patients with node-negative hormone receptor-positive breast cancer and intermediate 21-gene Recurrence Scores