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Under review as a conference paper at ICLR 2027

Statistical Risk Heads for Failure Warning Across Time-Series Forecasters

Abstract

Accurate time-series forecasting does not by itself specify when to issue a useful failure warning. This decision requires distinguishing approaching failures from normal operation while balancing missed events and false alarms. We introduce a statistical risk-head framework that adapts frozen forecasting models to failure warning using training targets that increase as failure approaches and degradation indicators computed from information available at prediction time. We train the risk heads using labels based on time remaining before failure, with additional losses that suppress high scores during safe operation, match changes in the target curve, and discourage falling risk as failure approaches. Warning thresholds are selected using training or calibration data. We evaluate the framework with DLinear, PatchTST, iTransformer, TTM, and FlowState on tiny-N-CMAPSS, NASA Battery Aging, XJTU-SY, and FEMTO/PRONOSTIA. Our system warns before more failures than a standard binary risk head in all 20 model–dataset pairs and improves 57 of 60 comparisons of event recall, false positive rate, and precision. Averaged equally across the 20 pairs, event recall increases from 65.98% to 87.35%, precision from 45.63% to 70.91%, and false positive rate decreases from 9.43% to 1.80%. These findings support statistical risk adaptation as a practical way to improve failure warnings across heterogeneous forecasting models.

Primary area:
learning on time series and dynamical systems
Keywords:
time-series forecasting, early failure prediction, predictive maintenance, statistical hypothesis testing, temporal supervision

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

This paper proposes risk heads that adapt frozen time series forecasters into failure detection systems. The method learns a bounded correction to a binary risk logit using features derived from observed history, forecast summaries, and forecast endpoints. Training uses temporally graded labels together with false-positive, smoothness, and monotonicity penalties in the loss function.

Critical strengths
  • The problem formulation is clear and practically motivated. The distinction between accurate forecasting and useful failure-warning decisions is important. The proposed framework is forecaster-agnostic and is evaluated with several forecasting models, which is a valuable design choice.

  • The bounded logit correction provides a simple and interpretable constraint on how much the risk head can alter the base binary predictor.

  • The controlled objective comparison in Table 2 is useful. In particular, the ablations indicate that the false-positive, smoothness, and monotonicity terms affect the recall–false-positive trade-off in meaningful ways.

  • The paper provides code and relatively detailed reproducibility information.

Critical weaknesses
  • The paper reports results for small evaluation cohorts on several datasets: seven eligible events for NASA Battery for example. Under these conditions, differences in caught events can be sensitive to individual trajectories. However, no confidence intervals, uncertainty estimates, or results over multiple training seeds are reported. This is important for assessing the robustness of the claimed gains.

  • The standard baseline definition seems a bit unfavorable as the input features, number of trainable parameters are not the same between standard and risk heads. Could it be a version of the baseline matching the full risk head in terms of these?

  • Appendix C.1 states that the calibration procedures differ from model to baselines. These different calibration targets and policies make the Table 1 system comparison harder to interpret, because they can substantially influence results. What is the reason for these different calibration settings?

  • The paper does not report typical selected values of the warning threshold (\eta). How much do calibrated thresholds vary across datasets, backbones, and folds? Are the selected thresholds systematically conservative or permissive? Since this setting concerns high-stakes and rare-event detection, some additional interpretability elements would be valuable.

Questions for authors

see weaknesses above

5 comments

We sincerely thank Reviewer aqs3 for the thoughtful and constructive review, and for the time given to our paper. We address each weakness below. We have incorporated these results into the revised paper and improved the main text so that it is easier to read.

Response to W1

We now report uncertainty for both result tables of the paper, as confidence intervals, a failure-by-failure test, and results over training seeds. Intervals are 95% and come from resampling whole assets 10,000 times, with each asset's predictions kept paired across both systems and all five forecasters.

Table 1. Change from the standard system to ours in the system comparison (percentage points, 95% CI).

DatasetFailuresEvent recallFPRPrecision
tiny-N-CMAPSS60+7.00 (3.00 to 11.00)−0.85 (−1.55 to −0.14)+1.86 (0.41 to 3.30)
NASA Battery7+37.14 (22.86 to 51.43)−4.12 (−6.90 to −1.48)+31.41 (17.84 to 44.62)
XJTU-SY15+21.33 (13.33 to 29.33)−6.50 (−9.38 to −3.81)+36.43 (26.92 to 45.81)
FEMTO17+20.00 (8.24 to 31.76)−19.04 (−27.58 to −11.24)+31.42 (22.41 to 40.13)
All 20 pairs99+21.37 (16.23 to 26.51)−7.63 (−10.16 to −5.21)+25.28 (19.62 to 30.91)

Every interval excludes zero, including on NASA Battery with its seven failures.

Table 2. Failure-by-failure comparison at the original cutoffs of the paper, and recall gain after removing the most favorable failures (percentage points). For each failure we count how many of the five forecasters caught it.

DatasetFailuresCaught by more forecasters with oursSameFewerRecall gainMost favorable failure removedTwo most favorable removed
tiny-N-CMAPSS6012471+7.00+6.10+5.17
NASA Battery7610+37.14+33.33+28.00
XJTU-SY151131+21.33+20.00+18.46
FEMTO177100+20.00+17.50+14.67
All four, removed from every dataset at once9936612+21.37+19.23+16.58

Only 2 of the 99 failures are caught by fewer forecasters with our system, against 36 caught by more. Under equal systems, the chance of a split at least this uneven is below 10⁻⁸ (exact sign test). With the two most favorable failures removed from NASA Battery, the gain there is still 28 points.

We retrained both heads with 10 seeds, and the whole pipeline, forecasters included, with 5.

Table 3. Results over training seeds, averaged over the 20 pairs (mean ± standard deviation, in %).

SeedsSystemEvent recallFPRPrecisionRecall gain
10, heads retrainedStandard head65.7 ± 1.69.5 ± 0.745.5 ± 1.5
10, heads retrainedOurs87.2 ± 0.91.8 ± 0.270.7 ± 1.2+21.5 ± 1.7
5, whole pipeline retrainedStandard head65.3 ± 2.19.6 ± 0.945.1 ± 1.9
5, whole pipeline retrainedOurs86.9 ± 1.21.9 ± 0.270.3 ± 1.5+21.6 ± 2.3

Table 4. Event recall by dataset over the 10 head seeds (mean ± standard deviation, in %).

DatasetStandard headOursGainLowest gain in any seedSeeds with higher recall
tiny-N-CMAPSS91.9 ± 0.699.0 ± 0.3+7.1 ± 0.7+6.010 of 10
NASA Battery39.4 ± 4.176.9 ± 2.6+37.5 ± 4.6+28.610 of 10
XJTU-SY61.2 ± 2.482.5 ± 1.7+21.3 ± 2.8+17.310 of 10
FEMTO70.3 ± 1.990.4 ± 1.5+20.1 ± 2.3+16.510 of 10
All 20 pairs65.7 ± 1.687.2 ± 0.9+21.5 ± 1.7+18.910 of 10

Our system is ahead in every seed on every dataset, and in at least 19 of the 20 pairs each time. The values in the paper lie within one standard deviation of the seed mean.

Table 5. Controlled objective comparison, full objective minus each alternative (percentage points, 95% CI).

AlternativeEvent recallFPRPrecision
Binary BCE, near horizon+19.14 (12.6 to 25.9)−5.39 (−7.3 to −3.6)+16.62 (11.4 to 21.9)
Binary BCE, full horizon+15.71 (9.8 to 21.8)−4.49 (−6.2 to −2.9)+14.13 (9.2 to 19.0)
Uniform label smoothing+13.57 (8.0 to 19.3)−4.03 (−5.6 to −2.5)+13.09 (8.4 to 17.8)
Class-balanced BCE+11.06 (5.9 to 16.4)−4.19 (−5.8 to −2.7)+14.74 (9.9 to 19.6)
Focal loss+9.63 (4.7 to 14.7)−3.44 (−4.9 to −2.1)+11.78 (7.2 to 16.4)
Temporal label smoothing+6.74 (2.7 to 10.8)−1.72 (−2.7 to −0.8)+6.00 (2.3 to 9.8)
Without false-positive penalty−2.22 (−5.0 to 0.5)−2.26 (−3.3 to −1.3)+5.74 (2.2 to 9.3)
Without shape-aware smoothness+5.06 (1.3 to 9.0)+0.13 (−0.4 to 0.7)+0.72 (−1.4 to 2.9)
Without monotonicity penalty+2.93 (0.3 to 5.7)−0.67 (−1.3 to −0.1)+2.24 (0.1 to 4.5)

The full objective beats every existing objective on all three metrics, and all 18 of those intervals exclude zero. It is also ahead of temporal label smoothing in all 10 seeds. The penalty rows match the roles described in the paper.

The result also does not depend on small cohorts. Our response to Reviewer frWU (W3) adds 12 datasets with 11,018 events.

Table 6. Events warned in time on the three largest new datasets and on all 12 (in %).

DatasetEventsStandard binary headOursGain (95% CI)
Los Alamos system outages6,96521.430.9+9.5 (6.3 to 12.7)
Alibaba rack incidents1,61835.248.6+13.4 (9.6 to 17.1)
Scania truck repairs43914.119.7+5.6 (2.1 to 9.1)
All 12 new datasets11,01833.742.7+9.0 (7.2 to 10.8)

Response to W2

We trained a standard head that receives exactly the inputs of our head and has the same number of trainable parameters. We also gave it the full 30-unit label, which removes the last difference in how the two heads are supervised.

Table 1. The standard head matched step by step to our head, averaged over the 20 pairs (in %). The baseline rows and the single-configuration row use the pooled 5% calibration level. The last row uses the calibration of the system comparison.

HeadInputsTraining labelParametersEvent recallFPRPrecision
Standard headforecast summary10 units1.2K to 2.9K65.989.4345.63
Standard head with our inputsforecast, history, physical limit10 units3.5K to 8.8K68.588.2148.36
Same, with our parameter countforecast, history, physical limit10 unitsabout 3K68.218.2748.13
Same, with the 30-unit label (fully matched)forecast, history, physical limit30 unitsabout 3K71.526.5853.12
Binary head inside our system, correction switched offforecast, history, physical limit30 unitspart of ours70.436.6152.88
Ours, single configuration of the controlled comparisonforecast, history, physical limitgradedabout 3K85.672.0666.99
Ours, system of the paperforecast, history, physical limitgradedabout 3K87.351.8070.91

Our inputs and parameter count raise the recall of the baseline by about two points, and the 30-unit label adds about three more. With the same pooled 5% calibration, our single-configuration head leads the fully matched baseline by 14.2 recall points and issues less than a third of its false warnings. The system of the paper leads it by 15.8 recall points (95% CI 10.2 to 21.5) and is ahead in all 20 pairs, so about three quarters of the gain in the system comparison remains. The same result appears inside our own system. Its starting logit is a binary head trained on the same inputs with the 30-unit label, and with the correction switched off it reaches the level of the matched baseline.

The parameter counts were close to begin with, 1.2K to 2.9K for the standard head and about 3K for ours. Table 2 varies the size of the fully matched baseline from a third of our parameter count to about three times as many.

Table 2. Event recall of the fully matched baseline at different sizes (in %).

Parameterstiny-N-CMAPSSNASA BatteryXJTU-SYFEMTOAll 20 pairs (recall / FPR / precision)
1K92.6751.4362.6772.9469.93 / 7.21 / 51.04
3K93.6754.2964.0074.1271.52 / 6.58 / 53.12
10K96.3354.2965.3376.4773.11 / 6.13 / 54.57
Ours, 3K99.0077.1482.6790.5987.35 / 1.80 / 70.91

The recall of the baseline rises by about 3 points over this range and stays more than 14 points below our head. A baseline somewhat smaller or larger than ours gives the same conclusion.

Table 3 matches the inputs in the other direction. It gives our head only the forecast summary, the input of the standard head, so each row compares the two heads on identical inputs and parameter counts.

Table 3. Both heads on identical inputs (event recall / FPR, in %).

Inputs of both headsStandard head, 30-unit labelOur head and objectiveRecall gain (95% CI)Pairs with higher recall
Forecast summary only68.72 / 8.1378.31 / 2.94+9.59 (4.28 to 14.97)18 of 20
Forecast, history, physical limit71.52 / 6.5887.35 / 1.80+15.83 (10.21 to 21.48)20 of 20

Our head is ahead on identical inputs in both rows, with fewer false warnings. The extra inputs add 2.8 points to the standard head and 9.0 points to ours. Giving the standard head our inputs removes only a small part of the difference. They become more useful through the graded target and the penalties, which is the method of the paper.

The controlled comparison in the paper is matched in the same way, since every objective is trained on our inputs with our head. Against temporal label smoothing, the strongest existing objective, our objective has higher mean recall at each of 10 head seeds. In a separate experiment with 50 runs on tiny-N-CMAPSS, it warned at least 20 flights ahead on 72.03% of failures against 65.47% (+6.57 points, 95% CI 2.33 to 11.20).

Reviewer_LbTMOpenReview ↗
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Paper summary

The paper turns the outputs of time-series forecasters into failure warnings. It argues that a small forecast error does not mean an approaching failure can be caught in time, and that a binary risk head does not use the temporal structure before a failure. The proposed risk head keeps the forecaster frozen and applies a bounded correction to the binary logit using forecast summaries, statistics of the observed history and optional degradation-boundary features. Temporally graded labels, a false-positive penalty, a smoothness penalty and a monotonicity penalty provide the training signal, thresholds are set on calibration data, and a bound is given for the size of the correction. Experiments cover five forecasters and four datasets, 20 pairs in total.

Critical strengths

S1. Cross-model consistency and rigorous ablation-based attribution. The framework is attached to five heterogeneous forecasters without changing their internal weights during risk training, and event recall improves on all 20 model–dataset pairs. The consistency of improvement across models is strong evidence that the framework is effective. In addition, the ablation study (Table 2) fixes the input features, the correction architecture, and the calibration rule, and gives the strongest baseline (TLS) the same graded targets. The additional gains over TLS can therefore be attributed to the proposed penalties, rather than to extra information or label–window matching. The ablation design and the attribution chain in the result analysis are fairly rigorous.

S2. Sound and complementary evaluation metrics. Rather than using point adjustment to treat a single local hit as detection of an entire event, the authors explicitly separate event-level recall from point-level false positive rate and precision. This makes the reported behavior more interpretable than the common practice in the anomaly-detection literature.

Critical weaknesses

W1. The paper reports no warning lead time for the proposed framework. In the experimental evaluation, an event is considered caught as long as a warning is raised once within the 30-unit window. Therefore, on the recall metric, a system whose first warning comes only one step before failure scores exactly the same as one that warns as soon as the window begins. The authors acknowledge this in Section 8: improved event recall does not imply longer warning lead time, their results do not measure this quantity, and they list "the fraction of failures detected with a specified minimum lead time" as future work. Appendix B provides a theoretical method for estimating warning lead time, but it is not applied in any experiment, and no lead-time values are reported. Warning lead time is, in fact, a key performance indicator for a warning system. Even if optimizing this quantity is left to future work, this key quantity should still be reported in the experimental results, in order to delineate the capability boundaries of the proposed framework.

W2. The paper reports no hyperparameter sensitivity analysis. First, in the Table 1 system comparison, the parameters of the proposed risk head undergo a "per-dataset candidate configuration selection" (whose individual candidate settings and selection criterion are not fully disclosed), whereas the baseline is presented with a fixed configuration and no comparable selection procedure is described. While this does not necessarily constitute data leakage, it limits attribution of the Table 1 gains; Table 2 provides a separate controlled objective comparison. Second, the paper neither provides hyperparameter sensitivity experiments nor fully discloses the experimental values of key hyperparameters. Empirical hyperparameter selection and sensitivity analysis are critical for assessing a method's stability and scalability, especially for a method with a relatively complex hyperparameter space (hmin⁡h_{\min}, γ\gamma, CC, ε\varepsilon, λ\lambda).

Questions for authors

Q1. Could you report the distribution of first-warning times relative to the failure time, and the fraction of failures detected with a specified minimum lead time? If the current experiments cannot produce them, what is the obstacle?

Q2. Could you disclose the specific criteria and results of the "per-dataset candidate configuration selection", and briefly analyze how the method's performance changes under different configuration choices?

Q3. Why do the nominal calibration targets differ across systems (5% vs 2.5% vs per-entity 5%/10%)? Do the conclusions hold under a unified calibration rule?

Q4. Which datasets enabled the optional physical branch? What is its ablation contribution? Without this information, the role of the physical branch in the experiments cannot be assessed.

8 comments

The authors have not yet responded to my comments, so I have decided to maintain my original score.

We sincerely thank Reviewer LbTM for the thoughtful and detailed review, and for the time spent on our paper. We address each weakness and question below. We have incorporated these results into the revised paper and improved the main text so that it is easier to read.

Response to W1 (and Q1)

We now report lead time in full. There was no obstacle. The saved scores already contain the first-warning time of every failure, so no model had to be retrained.

For each failure we recorded how many time units remained when the first warning was raised. Every model is set to the same realized false-positive rate of 2.5%, so an earlier warning cannot come from warning more often. A failure that was never warned counts as zero. TLS is temporal label smoothing.

Table 1. Share of failures with a first warning at least k time units before failure.

Systemk = 1k = 5k = 10k = 15k = 20k = 25k = 30
Standard binary system60.5%47.0%33.1%28.7%25.0%16.5%7.0%
TLS with our head74.0%57.0%35.5%31.0%27.0%18.0%7.8%
Ours90.0%70.0%49.7%48.3%44.0%40.4%27.1%
Gain of ours over standard+29.5+23.0+16.6+19.6+19.0+23.9+20.1
95% interval of the gain17.4 to 48.411.9 to 46.64.6 to 44.28.2 to 45.56.1 to 42.210.4 to 43.37.6 to 36.8

The k = 1 column counts any warning inside the window, the same definition as event recall in the paper. The k = 30 column counts only warnings raised as soon as the window begins. Our system warns on more failures at every lead time, and the relative gain over the standard system grows as the required lead gets longer. We computed the intervals by resampling whole assets and keeping their predictions paired across systems and forecasters. Every interval excludes zero.

Table 2 reports the systems exactly as submitted, at the original cutoffs of the paper.

Table 2. Share of failures warned at least 20 time units ahead, at the original cutoffs.

SystemWarned 20 units ahead
Standard binary system30.94%
Ours43.56%
Gain (95% interval)+12.62 points (1.88 to 23.92)

Table 3. Lead time of the first warning among caught failures, in time units.

System25th percentileMedian75th percentile
Standard binary system51326
TLS with our head5924
Ours51930

Table 4. Event recall and lead time, standard system against ours. Failures are grouped by which system caught them.

Group of failuresShare of all failuresMedian lead, standardMedian lead, ours
Caught by both systems59.5%1326
Caught only by ours30.5%n/a9
Caught only by the standard system1.0%6n/a
Caught by neither9.0%n/an/a
QuantityValue
Among failures caught by both, ours warns earlier64%
Among failures caught by both, same step21%
Among failures caught by both, ours warns later15%
Rank correlation between the recall gain and the gain in 10-unit warnings, over the 20 pairs0.74

On the failures that both systems catch, our first warning comes earlier in most cases, and the median lead is 13 units longer. The failures that only our system catches are the harder cases, which the standard system misses entirely, and our system warns on them a median of 9 units ahead. Across the 20 forecaster–dataset pairs, a larger gain in event recall comes with a larger gain in timely warnings. In our results, higher event recall comes with longer notice.

Table 5. Share of failures warned at least 10 time units ahead, by dataset.

Systemtiny-N-CMAPSSNASA BatteryXJTU-SYFEMTOAverage
Standard binary system69.0%28.6%30.1%4.9%33.1%
Ours84.0%14.3%64.0%36.5%49.7%

Table 6. Lead time by forecaster, averaged over the four datasets.

ForecasterStandard, warned 10 units aheadOurs, warned 10 units aheadGainStandard, median leadOurs, median lead
DLinear35.38%47.99%+12.611319
PatchTST33.61%48.35%+14.741319
iTransformer33.11%49.36%+16.251218
TTM31.00%52.60%+21.601319
FlowState32.40%50.20%+17.801319

Table 7. Lead time by training objective, all on our head.

ObjectiveWarned 10 units aheadMedian lead among caught failures
Binary BCE, near horizon31.8%8
Binary BCE, full horizon32.9%10
Uniform label smoothing33.4%10
Class-balanced BCE33.9%10
Focal loss34.6%10
Temporal label smoothing35.5%9
Full objective49.7%19
Without false-positive penalty45.8%18
Without shape-aware smoothness43.1%13
Without monotonicity penalty44.6%17

The gain is largest on the two bearing datasets. Our system gives a 10-unit warning about twice as often as the standard system on XJTU-SY and about seven times as often on FEMTO, and it adds 15 points on tiny-N-CMAPSS. On NASA Battery, Table 8 shows that our score separates from safe operation 27 to 29 cycles ahead, so the information is present and the 2.5% cutoff is the limiting factor on this dataset. The gain is positive for all five forecasters. The existing objectives differ little in lead time. The full objective gives the largest share and the longest median lead, and removing any one penalty lowers the share. Near-horizon cross-entropy has the shortest lead, as expected from its 10-unit training label.

We also applied the estimator of Appendix B. It finds the farthest lead at which the risk score before a failure can be distinguished from the scores of the same asset during safe operation. This is the earliest statistically detectable separation, and so the earliest point at which any cutoff could raise a warning. Following Appendix B, we tested every lead from 1 to 30 with 2,400 random relabelings at a 5% error level. As a control, we applied the same test to an earlier period in which each asset was still operating safely.

Table 8. Farthest lead at which the score separates from safe operation, and median lead of the first warning, in time units. A range gives the lowest and highest value across the five forecasters.

DatasetStandard system, farthest leadOurs, farthest leadOurs, safe-period controlOurs, median first warning
tiny-N-CMAPSS21 to 2330029
NASA Battery7 to 1027 to 2904
XJTU-SY10 to 1327 to 28024
FEMTO11 to 1428 to 2908

The control finds no separation on any dataset, so the result reflects the approach of a failure and not ordinary drift. Our score separates from safe operation at least 7 units earlier than the standard score on every dataset, and at least 14 units earlier on the three smaller datasets, so the head has information about the failure earlier. Our score also separates earlier than our own first warning on every dataset, so the same head can give earlier warnings with a different cutoff rule and no retraining. The farthest lead in Table 8 is the capability boundary of the present score, and the median first warning shows how much of it the current cutoff already uses.

In our response to Reviewer frWU, the smoothness penalty gives a lower bound on the score at each step of the warning window, which bounds how late the first warning can be.

Reviewer_frWUOpenReview ↗
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Paper summary

This paper studies how to adapt frozen time-series forecasters for failure warning. It combines forecast summaries and degradation features with a bounded risk correction, temporal label smoothing, and additional regularization. Experiments report improved event recall and fewer false alarms.

Critical strengths

Turning forecasting outputs into useful failure warnings is a practically relevant problem.

Critical weaknesses
  1. The framework combines established temporal label smoothing with degradation features, bounded residual correction, and several relatively straightforward penalties. The shape-aware and monotonicity terms also have overlapping effects. The paper does not sufficiently establish why this particular combination introduces a substantive advance over existing temporal supervision and lightweight adaptation methods.

  2. Although the forecasting backbones are reasonably varied, the comparisons mainly involve simple risk heads and alternative losses. Dedicated early-warning methods, dynamic survival models, RUL-based alarms, and simple physical-threshold or trend-based rules are missing.

  3. The datasets used in this paper is tiny, and much of the experimental analysis restates changes in the tables.

Questions for authors

see the weakness part

6 comments

We sincerely thank Reviewer frWU for the careful review and for the time and attention given to our paper. We address each weakness below. We have incorporated these results into the revised paper and improved the main text so that it is easier to read.

Response to W1

We ran a new experiment that changes one part of the method at a time and measures whether the two parts help more together than separately. The first part is the head. Ours is bounded, which means it starts from a binary risk score and may adjust it only by a limited amount. The second part is the training objective. Temporal label smoothing (TLS) gives each time step a target that grows as failure gets closer. Our objective uses the same targets and adds a false-positive penalty and two temporal penalties, smoothness and monotonicity.

We compared our head with a standard MLP head of about the same size, and our objective with TLS, which gives four models. The experiment uses the controlled setting of the objective comparison in the paper, where the bound applies on all four datasets. All four models use the same frozen forecasters, the same input features, the same training and test assets, and the same tuning budget. Every head receives the degradation features, so they cannot explain the differences. We fixed the realized false-positive rate at 2.5% for every model and counted the share of failures warned at least 10 time units before the failure. A missed failure counts as zero. The numbers are averages over five forecasters and four datasets.

Table 1. Share of failures warned ahead at a realized 2.5% false-positive rate.

HeadObjectiveWarned 10 units aheadWarned 5 units ahead
Standard binary system of the paperbinary33.1%47.0%
Standard MLP headTLS33.5%53.2%
Standard MLP headFull objective34.0%54.1%
Bounded head (ours)TLS35.5%57.0%
Bounded head (ours)Full objective50.4%71.3%

Table 2. Effect of switching from TLS to the full objective.

HeadChange in 10-unit warnings (points)Change in false-positive rate at the calibrated cutoffs (points)
Standard MLP head+0.5+1.04
Bounded head (ours)+14.9−1.72
Difference between the heads14.4 (95% CI 6.6 to 27.9), positive in 18 of 20 pairs2.76 (95% CI 1.01 to 4.50)

Our objective helps 14.4 points more with the bounded head than with the MLP head, and false alarms show the same pattern. We computed the intervals by resampling whole assets and keeping the four models paired. The full method gives 50% more timely warnings than TLS with a standard MLP head and 52% more than the standard binary system, and the ordering is the same at a 5-unit deadline. We also tried survival and multi-horizon objectives on our head, and a linear probe and an embedding adapter with our objective. None of them exceeds 35%.

The two parts help each other because of the bound. The head cannot change a decision that is already clear. If the base logit is more than C from the alarm cutoff, the decision stays the same. The objective can therefore change only decisions close to the cutoff, and for those the direction in which the score moves matters most. The two temporal penalties control that direction.

To test this explanation, we trained a version of our head with only the bound removed. It uses the same binary base score, residual network, features, objective, and training budget.

Table 3. Share of failures warned at least 10 units ahead with and without the bound.

HeadTLSFull objectiveGain from the full objective
Bounded head (ours)35.5%50.4%+14.9
Same head, bound removed35.0%41.5%+6.5
Effect of the bound+0.5+8.9 (95% CI 3.4 to 17.2), in 16 of 20 pairs+8.4

The bound adds 8.9 points under the full objective and almost nothing under TLS. Of the 14.4-point difference in Table 2, 8.4 points come from the bound and 6.0 from the rest of the head design.

The two temporal penalties have different roles. Consider two consecutive steps where the target risk increases by 0.05. If one model predicts an increase of 0.15 and another predicts a decrease of 0.05, both are 0.10 away from the target, so they receive the same smoothness penalty. In operation the first model only warns a little earlier than needed, whereas the second can switch off a warning that is already active. The monotonicity penalty separates these cases because it applies only when the score decreases.

The smoothness penalty affects when a warning starts. Let E be the total squared error in the score's step-to-step changes over a warning window, and let q be the target. Then the score at step j satisfies s_j ≥ s_1 + (q_j − q_1) − √((j−1)E). A warning is guaranteed at step j once the right-hand side reaches the alarm cutoff, and a smaller E makes this happen at an earlier step.

The monotonicity penalty affects whether a warning stays on. Let D be the total squared size of the score's downward moves over m steps where the target is rising. Then the score can drop by at most √(mD) over those steps, so a warning that starts with a margin larger than √(mD) above the cutoff stays on. In the final steps before failure the target is flat, and there the smoothness penalty limits any change.

Our measurements match this. The TLS loss contains no explicit penalty on how the score changes between consecutive steps, and its rising targets are the only influence on direction.

Table 4. Behavior of the score in the warning window.

ObjectiveSteps where the score falls while the target risesFirst warnings turned off before the failure
TLS31.4%29.3%
Full objective8.1%6.9%

A stronger smoothness penalty cannot replace the monotonicity penalty.

Table 5. Full objective with the monotonicity penalty removed and a stronger smoothness penalty (share of failures warned at least 10 units ahead).

Smoothness weightWarned 10 units ahead
1 times, monotonicity penalty removed44.6%
2 times, monotonicity penalty removed42.0%
4 times, monotonicity penalty removed39.5%
1 times, with the monotonicity penalty (full objective)50.4%

The monotonicity penalty also changes the minimizer of the loss, not only the size of the penalty. When the predicted changes are noisy, the best average rise becomes larger than the target rise, by (λ_mono/λ_smooth) × (|P|/|R|) times the expected size of a fall, where P is the set of all consecutive pairs and R is the set of pairs where the target rises. The score therefore rises faster as failure approaches, and no setting of the smoothness weight has this effect. Over the first half of the rising part of the window, the score rises 1.8 times as much as the target with the penalty and 0.9 times as much without it.

Response to W2

We added ten baselines that cover the four families of methods used for failure warning. Every baseline uses the same training and test assets, the same tuning budget, and the same calibration data as our method. We score them as in our response to W1, by the share of failures warned at least 10 time units ahead at a realized 2.5% false-positive rate. Ours is the system of the paper. Baselines that do not use a forecaster are averaged over five training seeds.

The first family is dedicated early-warning methods. A multi-horizon GRU learns from labeled failures and predicts whether a failure will occur within each of several future horizons, and two alarm methods raise an alarm when the forecaster's recent errors become unusually large (Hundman et al., 2018, and Siffer et al., 2017). The second family is dynamic survival models, which predict the distribution of the time to failure. We used Dynamic-DeepHit (Lee et al., 2020) and a discrete-time hazard model trained on exactly the inputs our head receives. The third family is RUL-based alarms, which predict the remaining useful life (RUL) and raise an alarm when it falls below a cutoff. We used the LSTM regressor of Zheng et al. (2017), tuned gradient-boosted RUL trees, and the adapter of Abdouni et al. (2026) in its original form, with frozen Chronos-2 embeddings. The fourth family is simple rules based on a physical failure limit. The limit rule raises an alarm when the degradation indicator comes within a fixed margin of the limit, and the trend rule raises one when a line fitted to recent values is projected to reach the limit within the warning window. These rules apply to the battery and bearing datasets.

Table 1. Share of failures warned at least 10 time units ahead, at a realized 2.5% false-positive rate. Rows are sorted by the last column, which includes every method.

MethodFull history, trained end to endAll four datasetsThree datasets with a physical limit
OursNo49.7%38.3%
Dynamic-DeepHit (Lee et al., 2020)Yes51.4%36.3%
Multi-horizon GRUYes50.6%35.4%
Trend ruleNon/a24.6%
Standard binary system of the paperNo33.1%21.2%
Discrete-time hazard model, same inputs as oursNo33.9%20.5%
Physical-limit ruleNon/a19.8%
Chronos-2 RUL adapter (Abdouni et al., 2026)No33.0%18.0%
Tuned RUL treesNo31.9%17.5%
LSTM RUL alarm (Zheng et al., 2017)Yes29.9%15.9%
Extreme-value alarm (Siffer et al., 2017)No22.7%14.2%
Forecast-error alarm (Hundman et al., 2018)No20.8%13.1%

Our head gives the most timely warnings of all methods on the three datasets with a physical limit, and it leads every method that does not train a full sequence model by more than 13 points in both columns. Averaged over all four datasets it is within 1.7 points of the two end-to-end sequence models, with about 5% to 6% of their trainable parameters. Those two models read the complete sensor history of each asset and are trained end to end for this task. Our head is attached to a frozen forecaster and receives only the most recent 8 to 16 observations together with summary features.

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