saturn-s2 — a synthetic pretraining corpus with events and precursors

saturn-s2 is Forgis/saturn-s plus one thing: events. The base corpus design is unchanged — same eleven-dimension design matrix, same two backbones, same observation models — and events are injected into each panel before the observation model, with per-window ground truth recorded.

Why it exists. Four self-supervised pretexts in a row failed to beat a matched random-init baseline on event forecasting, on a corpus that contained drift-like families and no events at all. What it never contained is the conjunction — a slow drift followed by an excursion — and that conjunction is the entire downstream task. This corpus supplies it.

"Strictly additive" is proved, not asserted. At p_event = 0 the builder reproduces the saturn-s builder byte for byte over every window, because events draw from their own RNG stream and every counterfactual replay restores the base stream. The test is in the repository.

patch tokens	99.9 M
windows	700,033
seed	3301
channels	1 – 64
events	96,653 over 700,033 windows
distinct realised event types	55 from 10 operators

The generator is a sampler, not a switch statement

MiniRocket spans an enormous function space with a small fixed kernel set plus random dilations and biases. This is the analogue for events: a small operator bank, each with a random parameterisation, composed one or two at a time. There is no branch per named event type — "bearing spall", "cavitation", "calibration drift" are points in a product space, not code paths. 55 distinct realised event types come out of 10 operators.

Every event is a point on four axes:

axis	ranges over
WHAT	the operator — which property of the generating process changes
WHERE	P = precursor channels, E = event channels, sampled independently
WHEN	onset, precursor lead, ramp shape, duration
HOW MUCH	amplitude in units of the affected channel's own sd

The operator bank, and its realised mass

operator	share of events
noise	0.138
level	0.138
variance	0.136
spectral	0.136
lag	0.136
gain	0.135
clip	0.135
acf	0.135
intermittent	0.135
coupling	0.089

coupling and lag change cross-channel structure with no marginal change at all — the event is visible only jointly. They are marginal-preserving by construction for the same reason NOISEFLIP and NPROLL are (arXiv:2606.02670): a cross-channel event that moves a marginal is not a cross-channel event.

Precursors

	measured
events with a precursor	0.801
…of those, P ∩ E = ∅ (precursor in a channel the event never touches)	0.194
…partial overlap	0.104
…P = E	0.702
precursors that ever become measurable	0.431

About the ~20% of events with no precursor. That is deliberate and it is grounded: two whole classes of real transition provably have no precursor of any kind — noise-induced tipping (Kuehn 2011, Thm 6.1) and rate-induced tipping, where the eigenvalue never moves (Ashwin et al. 2012, PTRSA 370:1166, Eqs 15–16). A corpus in which a precursor always exists is not testing forecasting.

About the disjoint share. It is the hypothesis this corpus exists to test, not a base rate it reproduces. Across eight standard multivariate anomaly benchmarks, 0 of 373 labelled segments are cross-channel-only (arXiv:2606.02670, Table 2); the authors conclude those benchmarks "are unsuitable for validating cross-channel modeling capabilities."

Per-window ground truth

column	meaning
event	0/1 — does an onset fall in this window
event_type	the operator(s), a+b for a composition, or none
onset_t	onset index within the window, −1 if none
precursor_start_t	when the precursor began to be injected
precursor_visible_from	the first index at which the precursor is MEASURABLE — see below
precursor_visible_from_p5	the same, requiring 5 consecutive crossings
lead_steps	onset_t − precursor_visible_from in panel coordinates — the real forecast horizon
lead_in_window	how much of that lead is observable from inside this window
precursor_present	1 if a precursor is active in this window even when no onset is
precursor_channels, event_channels	index lists; may be disjoint
event_amp_sd	amplitude in channel-sd units
precursor_type, n_ops, profile_shape, transient, overlap_mode, n_events_in_window	sampler provenance
*_latent	the same quantities measured before the observation model

precursor_visible_from has a definition, not a vibe

precursor_visible_from = min{ t : |lat(t)| > kappa * sd_local(t) },  kappa = 1.0

sd_local is the standard deviation of the pre-injection series over a trailing 128-step window (minimum 32). lat(t) = x_with_precursor(t) − x_without(t), measured after the observation model — so a precursor that a coarse quantiser destroys is correctly recorded as never having been visible.

Measured lead_steps distribution (over precursor-bearing events):

	steps
median	102
p90	293
p99	431
never became visible	0.569 of precursor-bearing events

Read this column with its caveat. At kappa = 1 a single-sample detector at α = 0.05 has power 0.26 — so the column marks a scale-crossing time, not a detectability time. Against a matched filter it under-states the horizon by up to ~4× for slow precursors and over-states it by up to ~2.2× for fast ones. And because it normalises by a marginal rather than a whitened sd, it is optimistic on the walk and longmem families by ((1+φ)/(1−φ))^(1/3) — 2.7× at φ = 0.9. It is a consistent, checkable definition; it is not a horizon a detector could realise.

Build gates

All thirteen. Gates 1–10 are the saturn-s auditor unchanged — events are additive to the corpus design, so a gate that passed for saturn-s and fails here would mean the injection broke something.

#	gate	threshold	verdict
1	dedup	0 duplicate windows	PASS
2	sd_floor	< 2% of windows below 1% of corpus SD	PASS
3	coupling	group_id recorded per PANEL (unique ids < windows), never index // F	PASS
4	rank_calibration	corr_erank_frac reaches the 0.11 corner (non-zero mass below 0.11) and spans to 1.00	PASS
5	clock_check	window-position probe at chance on injected events	PASS
6	leakage	zero real benchmark windows	PASS
7	coverage	>= 85% overall on the 18 features, CROSS >= 86%	PASS
8	channel_balance	effective C levels >= 6	PASS
9	family_balance	effective families >= 10.5	PASS
10	cross-channel coupling	differenced mean	r
11	event prevalence	fraction of windows with an onset OR a precursor in [0.15, 0.2]	PASS
12	precursor visibility	fraction of precursor-bearing events with lead_steps > 200 is >= 0.05	PASS
13	placebo / injection-artefact test	placebo AUROC < 0.55 (a zero-amplitude injection must be undetectable) AND control AUROC > 0.6 (the same detector must work on real events, or the placebo result proves nothing)	PASS

Gate 13 is the placebo test and it earns its place. Run the full injection pipeline at amplitude ~0 and require a detector to be at chance: measured 0.5044. It ships with a positive control — the same detector on real events reads 0.7320 — because a placebo test that passes with a broken detector is the absence of evidence, not evidence of absence. It failed on first run at 0.558 and the reason was worth finding: four operators were ignoring the amplitude knob entirely, so a third of the bank had no difficulty axis and a zero-amplitude event was still a real event.

Parameter provenance — 13 grounded, 15 chosen

This literature reports phenomenology ("variance rises before a transition") far more often than distributions ("variance rises by 2.9× over the last half of the approach"). So every parameter group is labelled, and a CHOSEN range is never presented as grounded.

13 of 28 generator parameter groups are sourced from published measurement; 15 are CHOSEN because no published number exists. A CHOSEN range is never presented as grounded.

The full ledger

parameter	status	source or reason
spectral.defect_orders	GROUNDED	Geometric formulas BPFO=(n/2)f_r(1-(d/D)cos phi) etc., Sensors 25(23):7371 Eqs 1-4, evaluated on published geometry: CWRU bearing data centre (primary), IMS via Sensors 24(11):3500 Table 2, XJTU-SY via Sensors 25(17):5347 Table 1.
spectral.sideband_spacing	GROUNDED	Structural identity for both gear mesh and bearing modulation; Sensors 24(8):2593 §2.1.
spectral.cwru_2xbsf_trap	GROUNDED	CWRU's published 'Rolling Element' column is 2*BSF (2x2.3567=4.7134 vs published 4.7135). A ball defect strikes both races once per ball revolution. Sampling that column directly would be a factor-of-2 error.
acf.phi_target_rising	GROUNDED	Dakos et al. 2012 PLoS ONE 7:e41010 Fig. 2: lag-1 autocorrelation rises ~0.78 -> ~0.95 on the raw series approaching a fold, Kendall tau 0.911. Graphical read-off; the paper prints tau but not endpoint magnitudes.
acf.phi_target_falling_branch	GROUNDED	Kuehn 2013 Figs 13-14: the same bifurcation yields autocorrelation and variance moving up, flat or DOWN depending only on the multiplicative noise structure. A corpus whose indicator always rises would train a detector the literature says does not exist.
variance.k_rising	GROUNDED	Dakos 2012 Fig. 2: SD rises ~1.7x (variance ~2.9x) over a fold approach, Kendall tau 0.939.
variance.k_falling_branch	GROUNDED	Dakos 2012 Fig. 2H: in the flickering regime SD rises then FALLS, Kendall tau only 0.208. Plus Kuehn 2013 Figs 13-14 as above.
event.no_precursor_share	GROUNDED	Two whole event classes provably have no precursor of any kind: N-tipping (Kuehn 2011 Thm 6.1) and R-tipping, where the eigenvalue never moves (Ashwin et al. 2012 PTRSA 370:1166, Eqs 15-16, §3.1). A corpus in which a precursor always exists is not testing forecasting.
lag.marginal_preserving	GROUNDED	arXiv:2606.02670 Table 3: NOISEFLIP and NPROLL, two marginal-preserving corruptions, are the only validated positive controls for cross-channel-only anomalies (99.2% correctly classified over 24,000 trials). This operator is the smooth analogue of NPROLL; a circular roll would leave a wrap discontinuity that gate 13 would flag as an artefact.
coupling.marginal_preserving	GROUNDED	Same requirement as above: the cross-channel change must be invisible in every marginal. An orthogonal rotation of two independent equal-variance channels leaves them uncorrelated -- measured moving correlation 0.003 -> 0.001, i.e. doing nothing.
clip.quantile_parameterisation	GROUNDED	THEORY.md D6: a rail outside the observed range is a no-op, so the threshold must be parameterised by the channel's own distribution rather than by an absolute scale.
spectral.freq_floor	GROUNDED	THEORY.md D4: a line below ~2 cycles per context window is indistinguishable from level. The eval context is 512 steps.
acf.phi_ceiling	GROUNDED	THEORY.md D5: phi -> 1 is indistinguishable from the random-walk BASE family; bound (1-phi)*W >= 3 at W=512.
event.amp_range	CHOSEN	NO NUMBER IN LITERATURE. Run-to-failure studies (IMS, XJTU-SY, FEMTO) report raw g, or [0,1]-normalised health indices, or figures with unlabelled axes; no source gives a healthy baseline and a peak as numbers in sd units. The range is chosen to span sub-threshold to obvious so that difficulty is a continuum. Nothing was converted.
event.lead_range	CHOSEN	NO NUMBER IN LITERATURE for an absolute lead-time distribution. The literature reports lead as a FRACTION of run length (IMS indicator knees at 0.748-0.845 of run, n=3; Severson battery predictive at cycle 100 of 150-2300). 480 is set by our own eval context of 512: a lead longer than the context cannot be observed and so is not a forecast horizon. This is a defensible choice but it is a choice, and it is the same class of decision as the previous corpus's U(230, 421), which was reverse-engineered from our own scoring band.
spectral.sideband_ratio	CHOSEN	NO NUMBER IN LITERATURE. Four gear-crack papers report sideband PRESENCE and modulation index TRENDS; none reports a sideband-to-carrier amplitude ratio.
spectral.n_sidebands	CHOSEN	No published distribution over sideband counts.
lag.delta_max	CHOSEN	NO NUMBER IN LITERATURE for lead-lag drift magnitudes.
noise.amp	CHOSEN	No published distribution for sensor noise-floor degradation magnitude.
intermittent.p0_p1	CHOSEN	No published distribution for burst-rate change.
intermittent.burst_w	CHOSEN	No published source.
gain.k	CHOSEN	No published distribution for sensitivity-change magnitude.
clip.quantile_range	CHOSEN	The parameterisation is grounded (D6); the endpoints are not.
event.p_two_ops	CHOSEN	KernelSynth (Chronos §4.2, Algorithm 2) composes j ~ U{1,5} primitives, so composition depth is a validated architecture, but the specific probability is ours. THEORY.md shows depth 3 is provably needed for arbitrary cross-channel covariance and we ship depth 2.
event.p_disjoint	CHOSEN	NO NUMBER IN LITERATURE -- and the honest reason is stronger than that. arXiv:2606.02670 finds ZERO of 373 labelled segments across eight standard multivariate anomaly benchmarks are cross-channel-only. So there is no empirical base rate to match: this share is the HYPOTHESIS the corpus exists to test, not a fact it reproduces.
event.coh_bias	CHOSEN	The NEED for it is proved (THEORY.md Prop 15: if E is drawn independently of anything observable, the precursor carries provably zero information about WHERE the event lands). The exponent is ours.
event.p_event	CHOSEN	Calibrated on a pilot to land the MEASURED prevalence inside the pre-registered gate-11 band [0.15, 0.20]. A calibration to hit a declared design target, not a tuned result.
event.profile_shapes	CHOSEN	The accelerating exp shape is motivated by the bifurcation-approach phenomenology, but no source gives a distribution over onset profile shapes.

Could not verify (each was tried and failed, and nothing was allowed to stand in):

• Randall & Antoni MSSP 2011 (10.1016/j.ymssp.2010.07.017), Antoni MSSP 2006, Lei et al. MSSP 2018 -- all closed access. Every claim resting on them was re-grounded in open sources or dropped.
• Dakos et al. 2008 PNAS per-dataset Kendall tau values -- blocked on every route tried.
• FEMTO/PRONOSTIA bearing specifications entirely -- HAL bot-check and IEEE paywall. Nothing was allowed to stand in for this row.
• Ditlevsen & Johnsen 2010's exact statistic and p-value -- paywalled; the '17 events, no significant EWS' count is attributed via Hummel et al. 2025 ESD 16:2035 §1, not read in the original.
• KL closed forms for variance / AR(1) / spectral changes. The CUSUM delay MECHANISM (delay ~ log(1/alpha)/KL) is verified; the per-operator divergences are not sourced, so difficulty is NOT equalised across operator types via KL.

Not cited anywhere, because it could not be resolved to any identifier:

• Lai et al., 'Revisiting Time Series Outlier Detection', NeurIPS 2021 Datasets & Benchmarks -- could not be resolved to an arXiv ID or DOI, so it is not cited anywhere.

What this corpus does NOT contain

The operator bank's reachable set is characterised exactly, and eight classes of distributional change are provably outside it: copula/tail-dependence change at fixed marginals and correlation; chaotic dynamics change (a support-dimension obstruction — depth does not help); higher-order-only structure such as a bispectrum change at fixed power spectrum; latent regime dynamics that are not a gate; non-stationarity outside the profile dictionary, including "the process became long-memory"; conditional heteroskedasticity (GARCH); and nonlinear cross-channel dependence. Within the stationary Gaussian sector the bank is dense in spectral density as composition depth grows; at the shipped depth of 2 it is a finite-dimensional family. This is a coverage argument, not a universality theorem.

Also not implemented, each a real gap: a KL rejection sampler to reject degenerate and unresolvable draws; a depth-3 (coupling, gain, coupling) stratum; whitened precursor visibility; a regime operator; a per-panel Bayes-rate difficulty label; event-time label jitter matched to the ~±3.5% spread real detectors disagree by; and a MiniRocket-versus-Bayes triviality gate.

Relationship to the other saturn corpora

corpus	events	use
Forgis/saturn-s	no	the event-free control; exp-38/39/40/41 are reproducible against it
Forgis/saturn-s2	yes	this corpus
Forgis/saturn-m	no	larger, event-free

saturn-s and saturn-m are not modified. Any comparison between saturn-s and saturn-s2 changes exactly one variable.