When Can Survivors Stop Being Watched? Era-Aware Residual-Risk Rules for Ending Second-Cancer Surveillance

Cancer survivors are usually followed closely for about five years and then discharged. Registry studies show this timing is often wrong. After pelvic radiotherapy for rectal cancer, secondary bladder cancer risk peaks more than 20 years later, and ovarian cancer risk also peaks after 20 years. Among long-term survivors of nasopharyngeal cancer, deaths from causes other than cancer overtake cancer deaths after about a decade. We propose to turn decades of registry follow-up into a stopping rule. For a survivor who is still alive and free of a second cancer at year $s$, we estimate how much second-cancer risk remains in the next few years beyond what an age-matched member of the general population already carries. Specialized surveillance ends once that excess risk falls below a clinically chosen threshold, after which ordinary population screening covers the patient.

The hard part is that the only data long enough to show 20-year latencies come from patients treated in the 1970s and 1980s, with radiotherapy techniques that no longer exist. The main methodological contribution is to model the second-cancer hazard as a function of both time since treatment and treatment era. We then test honestly, by backtesting on patients treated later, whether late-risk estimates from old eras can be carried over to modern patients. We also report how much the stopping year depends on that carry-over assumption.

Core Claim

Deciding how long to watch a survivor is mainly a question about the residual risk of a second cancer, conditional on having survived to that point. It needs to be answered with competing-risk methods, in excess-over-population units, and with era made explicit. Existing registry studies report risk measured from the date of diagnosis. Risk and Prognosis of Secondary Bladder Cancer After Radiation Therapy for Rectal Cancer and Association of Radiotherapy for Rectal Cancer and Second Gynecological Malignant Neoplasms both report cumulative incidence from diagnosis, pooled over 1973–2015. Neither estimate answers the question a clinician faces at year 8: "given this patient is here and cancer-free now, is continued specialized follow-up still worth more than routine care?"

Our target quantity is the landmark excess yield. Take a survivor with covariates $x$ (age, sex, treatment, and treatment era $e$) who is alive and free of a second primary at landmark time $s$. For a window of length $w$, the excess yield is

$$\Delta(s,w \mid x) = R(s,w \mid x) - E(s,w \mid x).$$

Here $R$ is the probability of a second primary in $(s, s+w]$, estimated so that death from other causes removes the patient from risk rather than being treated as ordinary censoring. $E$ is the probability expected from age-, sex- and calendar-matched population incidence over the same window. The rule is to stop specialized surveillance at the first $s$ after which the upper confidence bound of $\Delta$ stays below a threshold $\delta$. We report results for a range of $\delta$ rather than committing to one value.

The claim is falsifiable in two ways. First, era-aware estimates of $\Delta$ must be better calibrated on later-treated patients than pooled estimates. Second, the implied stopping years must differ materially from both the five-year convention and from rules read off pooled, from-diagnosis cumulative incidence curves.

Research Program

The primary setting is the rectal cancer cohorts drawn from the Surveillance, Epidemiology, and End Results (SEER) 9 registries, 1973–2015. These cohorts are the setting of the two Guan et al. studies above, with secondary bladder and gynecological cancers as outcomes. The second setting is the SEER-17 nasopharyngeal cohort from Cause of death during nasopharyngeal carcinoma survivorship. In that cohort the competing-mortality side dominates, so the rule is stressed in a regime where most survivors die of something else before any second cancer appears.

The first component is a landmark competing-risk model. At landmarks $s = 1, 2, \dots, 25$ years, we restart the clock for everyone still at risk. We then fit Fine-Gray subdistribution models for the second primary, which keep patients who died of other causes in the risk set so that their deaths are not treated as ordinary censoring. We also fit cause-specific models for death from the index cancer and from non-cancer causes. Coefficients are allowed to vary smoothly in $s$. This reuses the competing-risk machinery that Guan et al. and Characteristics and Outcomes of Second Primary Multiple Myeloma in Adult Cancer Survivors already apply, but asks a conditional question instead of a from-diagnosis one.

The second component is era structure. Treatment era enters as a smooth effect with an era-by-latency interaction. The key assumption is that the era effect estimated at latencies observable for all eras, roughly the first 10–15 years, carries over to longer latencies. We cannot verify this assumption directly for recent eras. We therefore test its analogue on older eras and report stopping years under the carry-over assumption alongside bounds that relax it. The temporal-confounding literature in the file motivates this component. Aftahy et al., Yue et al. and Bai et al. document how secular improvements in care and learning curves bias comparisons across eras. For defining time zero we follow the concerns about immortal time and generalized propensity scores for era raised by Kiciman et al. and Mishra-Kalyani et al..

The third component is a confounding adjustment for the treatment contrast. Radiotherapy is not assigned at random, so any radiotherapy-specific rule uses inverse-probability weighting on registry baseline covariates, in the style of Long-Term Survival in Men With High Grade Prostate Cancer. We state clearly what this cannot fix. The registry lacks smoking history, radiation dose, and germline status, and both Guan papers and Second primary malignancies in cervical cancer and endometrial cancer survivors flag these gaps. Where the stopping year is sensitive to the treatment effect, we report sensitivity to unmeasured confounding.

The scope is deliberately limited. We estimate the risk side of the surveillance decision, not the benefit of earlier detection. The 2-MM paradox in the multiple myeloma study shows that registry survival differences after surveillance-detected cancers can reflect lead time. In that study, second primaries had lower myeloma-specific mortality (SHR 0.848) but shorter overall survival (41 vs 48 months). Registry survival therefore cannot credibly supply the benefit term.

Baselines

The naive reference point is the fixed five-year discharge that the file describes as current practice. We score it by the fraction of observed excess second primaries that occur after year 5 among patients still alive at year 5. For the gynecological outcome, the file reports that ovarian risk peaks after 20 years, so we expect this fraction to be large.

The strongest existing method is the pooled Fine-Gray cumulative incidence analysis of the Guan bladder study. It reports a 30-year-scale cumulative incidence of 1.85% with radiotherapy versus 1.24% without, an adjusted HR of 1.443 (95% CI 1.209–1.720), and an SIR of 1.35. The gynecological study reports a 30-year cumulative incidence of 4.53% versus 1.53%. We rebuild these analyses on the same SEER extract and check that we reproduce these figures within sampling error. We then derive a stopping year from them by differencing the pooled cumulative incidence curves in windows of length $w$. The same data, covariates, and threshold $\delta$ are used for both approaches, so the only differences are conditioning on landmark survival and modeling era. Beating this baseline means better calibration of the windowed yield on held-out later eras, and a stopping year whose confidence interval excludes the pooled estimate in at least one outcome. No reported result was found on Lacuna for the calibration of conditional residual risk from these pooled models, so this comparison is new.

A flexible-predictor baseline replaces our structured model with SurvivalPFN, a pretrained survival model that makes predictions from a dataset supplied in context. It is fit on the same landmark data without explicit era structure. The file reports only that SurvivalPFN achieves the best median rank over 61 held-out datasets; no reported per-dataset numbers were found on Lacuna. Two ablations isolate the key ingredients: removing the era terms while keeping landmarking, and removing landmarking while keeping era. A further check replaces Fine-Gray with Kaplan-Meier estimates that treat competing deaths as ordinary censoring, to quantify how much that choice inflates residual risk and delays stopping.

Why not just…?

Why not just read the stopping point off existing cumulative incidence curves? This is the real competitor, and the ablation settles it. Curves measured from diagnosis mix together patients who died early with those who survived, and they pool 1973 radiotherapy with 2010 radiotherapy. If era-aware landmark estimates give the same stopping years and no better calibration on later eras, we will report that the simple approach is adequate for this question.

Why not just learn an optimal dynamic surveillance policy with censored Q- or O-learning? Constructing Stabilized Dynamic Treatment Regimes for Censored Data learns sequential rules from right-censored data. It reports a mean survival of 14.67 versus 5.73 in simulations where the outcome model is misspecified. Those rules need recorded decisions and their consequences. SEER records no surveillance visits, and survival after detection is contaminated by lead time. A learned policy would therefore rest on quantities the data cannot identify. The DTR machinery becomes appropriate once linked imaging and visit data exist, for example from the ARILIS cohort.

Why not just use a flexible machine-learning survival model? It may predict well within an era. However, it has no mechanism for extrapolating to latencies that recent eras have not yet reached. The backtest described below measures whether this matters.

Why not keep the five-year rule and add generic primary-care screening? That is exactly what our rule recommends once $\Delta$ falls below $\delta$. The question is when that point arrives, and the latency peaks reported in the file suggest it is well after year 5 for some organs.

Proposed Experiments

The decisive check is a temporal backtest. We fit on patients treated from 1973 to 1985 and predict windowed excess yields at latencies of 5–20 years for patients treated from 1986 to 1995, whose outcomes are observed. We compare the observed-to-expected ratio and the windowed Brier score across our model, the pooled baseline, and SurvivalPFN. If the era-aware model does not beat the pooled model here, we do not trust its extrapolation to modern patients either.

We then report stopping years by outcome (bladder, uterine corpus, ovary), by age group, and by treatment. For each rule we also report the number of surveillance-years it saves or adds, and the number of excess second primaries that occur after its stopping point, relative to the five-year rule.

In the nasopharyngeal cohort we check the competing-mortality side. The test is whether non-cancer deaths make $\Delta$ fall below $\delta$ early. If they do, the result supports redirecting follow-up toward cardiovascular and infection risk, as argued by the ARILIS protocol.

Finally, a sensitivity analysis to unmeasured confounding on the radiotherapy effect shows how strong a hidden confounder such as smoking would need to be to move the stopping year by five years.

References

  1. Risk and Prognosis of Secondary Bladder Cancer After Radiation Therapy for Rectal Cancer: A Large Population-Based Cohort Study
  2. Association of Radiotherapy for Rectal Cancer and Second Gynecological Malignant Neoplasms
  3. Cause of death during nasopharyngeal carcinoma survivorship: a population-based analysis
  4. Characteristics and Outcomes of Second Primary Multiple Myeloma in Adult Cancer Survivors: A Population‐Based Cohort Study
  5. The Impact of Postoperative Tumor Burden on Patients With Brain Metastases
  6. Survival analysis of patients with non-small cell lung cancer who underwent surgical resection following 4 lung cancer resection guidelines
  7. Clinical outcome of laparoscopic versus robot-assisted radical cystectomy for patients with bladder cancer: a retrospective study
  8. Answering What If, Should I, and Other Expectation Exploration Queries Using Causal Inference over Longitudinal Data
  9. Estimating the palliative effect of percutaneous endoscopic gastrostomy in an observational registry using principal stratification and generalized propensity scores
  10. Long-Term Survival in Men With High Grade Prostate Cancer: A Comparison Between Conservative Treatment, Radiation Therapy and Radical Prostatectomy—A Propensity Scoring Approach
  11. Second primary malignancies in cervical cancer and endometrial cancer survivors: a population-based analysis
  12. SurvivalPFN: Amortizing Survival Prediction via In-Context Bayesian Inference
  13. Constructing Stabilized Dynamic Treatment Regimes for Censored Data
  14. Using artificial intelligence to predict and prevent non-cancer mortality in patients with cancer: ARILIS study protocol