Public health agencies summarize decades of disease rates with joinpoint regression. The method fits a chain of straight lines to, usually, the log of a rate over time, with the lines meeting at "joinpoints" where the slope changes. Each segment is then reported as an annual percentage change. The most policy-relevant question is whether the trend has changed in the last few years. By construction, standard practice cannot answer it. Joinpoint software forbids knots within roughly two to four observations of either end of the series. On a Global Burden of Disease series with 32 annual points, that leaves the latest years unmonitored. If the ban were simply dropped, a knot at the second-to-last year would amount to a hinge fit to one or two points. A reporting revision in the final year could then produce a "trend change."
This proposal treats the end of a short series as its own inference problem rather than as a margin to trim. We first compute exactly, with no asymptotics, how large a slope change must be to be detectable at each distance from the end. We then build a scan test whose false-alarm rate is controlled separately at every candidate position, including the last few. It is calibrated against a null model that includes serially correlated errors and occasional endpoint revisions. Finally, instead of forcing a point estimate of a knot location that the data cannot support, the method reports a confidence set: for example, "the slope changed at some year in 2018–2020, with post-change annual percentage change between X and Y." The core claim is that boundary failures in joinpoint regression come from two sources. One is that an edge hinge cannot be told apart from an endpoint outlier. The other is that errors are autocorrelated. They do not come from test-statistic variance, which is what step-change boundary corrections target. Handling these two causes directly yields a usable detector for recent changes whose error rates are known.
Where the gap actually is
Boundary bias in change-point detection is well documented for step changes. Vert and Bleakley showed, for group-penalized piecewise-constant fits, that detection power peaks in the middle of the series and collapses near the edges above a critical noise level. They proposed a position-dependent correction but never implemented it. Lung-Yut-Fong et al. corrected rank statistics for the imbalance in sample size between the two sides of an edge split. Sinn et al. found that kernel two-sample discrepancies drift toward sequence edges and added a penalty to counter it. Toutounji and Durstewitz came closest to our setting. Their method, PARCS, converts step changes into kinks by taking a cumulative sum and then fitting adaptive regression splines, which cut median center bias from 4 time steps to 1. These papers motivate the proposal: they establish that edge positions need their own treatment. None of them handles series whose raw form is already continuous and piecewise linear. PARCS explicitly requires manual detrending when a slope is present.
The joinpoint side supplies the model but not the edge inference. Acharya et al. made segmented regression fast. They evaluated only overall squared error, not where knots land near the ends. At the n ≈ 30 of registry work, speed is not the bottleneck anyway. Wang et al. achieved near-optimal localization rates for regression change points. Those rates are asymptotic, and their interval-drawing scheme itself imposes minimum lengths near the boundary. Nie and Nicolae constrain our design in a useful way. They proved that estimators built for abrupt changes converge to the midpoint of a gradual ramp. So we fit hinges directly rather than repurposing mean-shift detectors, and we report sets rather than points when the transition may be smooth. Applied papers show the pattern we want to fix: they fit joinpoints to GBD series of 32 years (Zhang et al. 2026, Mu et al. 2025) and to SEER series (Kadeerhan et al.), and none reports anything about the final years except as part of the last admissible segment.
One observation drives the design. For a fixed candidate knot $\tau$, the ordinary F statistic for adding the hinge $(t-\tau)_+$ is already standardized. Under Gaussian independent errors, it has the same exact distribution at every position. So the variance-imbalance corrections from the step literature fix a problem that the Gaussian F test does not have. The edge problem lies elsewhere. As $\tau$ approaches the last observation, the hinge regressor becomes nearly an indicator of the final point or two. The hinge test then becomes an outlier test, and it is extremely sensitive to the tails of the endpoint noise, to reporting revisions, and to autocorrelation. Its power to detect a genuine slope change also shrinks rapidly.
Research Program
The first component is an exact detectability curve. For a design with $n$ time points, $K$ existing knots and a candidate hinge at distance $d$ from the end, we write $\beta_d$ for the hinge coefficient, that is, the slope change. Its least-squares estimate has variance $\sigma^2 v_d$, where $v_d$ is the corresponding diagonal element of $(X^\top X)^{-1}$ and $\sigma^2$ is the noise variance. The minimum slope change detectable with power $1-\gamma$ at level $\alpha$ is then
$$\delta_{\min}(d) = \sigma \sqrt{v_d}\,\big(z_{1-\alpha/2} + z_{1-\gamma}\big),$$
where $z_q$ denotes the standard normal quantile. The normal quantiles come from the exact Gaussian sampling distribution of the estimate. Under AR(1) errors, $v_d$ is replaced by the sandwich form using the error covariance. Converting $\delta_{\min}(d)$ into annual-percentage-change units gives a table that registries can read directly. For a GBD-length series, it states how large a change in the last three years could possibly be seen. This is a small but missing, non-asymptotic result, and it lets the method decline to answer when the data cannot answer.
The second component is a boundary-calibrated scan test. We fit the null model with $K$ knots, estimated as in standard practice away from the edges. We then generate replicate series from that fit under a noise model with three parts: AR(1) Gaussian errors, a heavy-tailed revision term that affects only the final one to two observations, and optional Poisson overdispersion for count data. The parameters of the revision term are estimated from the registry itself, by comparing successive GBD releases (2019 against 2021) of overlapping years. For every candidate position in the last $m$ points, we compute a position-specific critical value from these replicates. The per-position false-alarm rates are then equal and sum to the target level. This is the correction Vert and Bleakley proposed but never implemented, here calibrated to the real failure mechanism.
The third component is set-valued reporting. A confidence set for the knot location comes from inverting the per-position tests. A confidence interval for the post-change annual percentage change is formed jointly over that set. When the set spans an interior year and the edge, the method says so rather than committing to a location.
Baselines
The naive reference point is standard practice: grid search with a boundary exclusion of three observations and knot count chosen by permutation test or the Bayesian information criterion. This is how the cited GBD and SEER analyses are run. It cannot detect recent changes at all, so its power in the last three years is zero by construction. Its value as a baseline is on interior knots and on how well the confidence intervals for the final-segment annual percentage change cover the truth.
The strongest direct competitor is the same procedure with the exclusion reduced to one observation. Here knots are chosen by exact dynamic programming, which is trivially cheap at n ≈ 30 and so removes any speed argument (Acharya et al. is relevant only for long series). Selection uses either a single sup-F threshold from permutation or the Bayesian information criterion. It is the fairest competitor because it differs from our method only in calibration.
A third baseline converts the problem to step changes. We take first differences of the log rate, so that slope changes become mean shifts, and apply PARCS and CUSUM, the cumulative-sum scan. For PARCS, no Lacuna-reported number on joinpoint data exists. The only reported figure is median center bias of 4 steps for CUSUM versus 1 for PARCS on synthetic step series (Toutounji and Durstewitz).
For gradual transitions, the max-gap estimator of Nie and Nicolae is included as the onset-focused competitor.
Two ablations isolate what matters: position-specific critical values versus a single pooled threshold, and a Gaussian independent null versus the null that includes revisions and AR(1) errors.
All methods get the same series, the same maximum number of knots, and the same Monte Carlo budget for calibration (10,000 replicates per series). No method may tune on the held-out truncation years. Beating the strongest competitor means two things. First, false alarms in the last $m$ points must stay within 1.5 times nominal, where the one-observation-exclusion baseline is expected to inflate. Second, power at matched false-alarm rate must be at least as high, and the confidence intervals for the final-segment annual percentage change must reach nominal coverage. No Lacuna-reported result was found for boundary knot localization or false-alarm rates on GBD or SEER series.
Why not just…?
Why not just keep the boundary exclusion? It is honest about false alarms but blind to exactly the years policy cares about. Li et al. and Daly et al. both describe the resulting blackout window as a real operational cost. Our detectability curve also shows how much of that blindness is unavoidable. If $\delta_{\min}$ in the last two years exceeds any plausible epidemiological change, we will report that trimming was right for that horizon. We consider that a legitimate outcome.
Why not just shrink the exclusion to one point and use the usual permutation test? This is the real threat. If a permutation or Gaussian sup-F threshold already controls edge false alarms on realistic data, our calibration adds little. The pure permutation null fails for two reasons: it destroys trend structure, and it ignores that revisions concentrate at the end. We will test this directly. The ablation that swaps our null for the Gaussian independent one, evaluated on series generated with revision noise estimated from successive GBD releases, settles the question. If the two tests have indistinguishable per-position false-alarm rates there, the contribution shrinks to the detectability analysis, and we will say so.
Why not just difference the series and use a step-change detector like PARCS? Differencing doubles the noise variance and introduces negative serial correlation. The cumulative sum of the differences also reduces to the original series minus the line joining its first and last points. That anchors the transformed series on the very endpoint whose reliability is in question. Our argument therefore predicts that PARCS-on-differences will be more sensitive to final-year revisions than a direct hinge fit. The synthetic revision experiments will confirm or refute this.
Why not just use a robust loss? A Huber or rank-based fit, in the spirit of Lung-Yut-Fong et al., down-weights the final point. That removes the ability to tell a single-point anomaly from the start of a new slope, but does not resolve the ambiguity. We include a Huber variant of the scan as a baseline. It should trade false alarms for lost power in the last two years, and the power curves will show by how much.
Proposed Experiments
The synthetic study mirrors registry designs: n = 20 (SEER-length) and n = 32 (GBD-length), zero to three interior knots, and one optional change at distance $d \in \{1,\dots,6\}$ from the end. The slope change is swept from zero up to three times the theoretical $\delta_{\min}(d)$. Transitions are either sharp or ramped over three years, the latter to reproduce the midpoint effect of Nie and Nicolae. Noise is Gaussian, AR(1) with correlation up to 0.6, overdispersed Poisson, and each of these plus endpoint revisions. We measure four things: false alarms at each position under no recent change, power as a function of $d$ against the theoretical curve, localization error and confidence-set coverage, and coverage and bias of the final-segment and average annual percentage changes.
The decisive real-data check is truncation backtesting on GBD 2021 series of the kind analyzed in Zhang et al. 2026, Mu et al. 2025, and Guo et al. 2025, and on SEER series. We truncate each series at year T and run every method on the truncated data. The resulting edge calls are scored against pseudo-truth. Pseudo-truth is defined as knots the full series places strongly, meaning they are significant under standard software and at least five years from both full-series ends, that fall in the last years before T. Spurious edge calls are those the full series does not support. Two further checks complete the design. Scoring GBD 2019 against GBD 2021 values of the same years tests directly whether edge knots called on the older release survive revision. The 2020–2021 pandemic years provide a stress case at the very edge, where a level shock rather than a slope change is expected. The proposal succeeds if, on backtests, the calibrated scan recovers truncated-edge knots that the standard exclusion misses, while holding spurious edge calls near nominal where the one-point-exclusion baseline does not. The detectability curve should also predict which truncated knots were recoverable at all.
References
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