ROGII Wellbore Geology Prediction — Working Note Team: Malyshev Danil
One-paragraph summary. We predict the true vertical thickness (TVT, stratigraphic position) of the unlabeled toe of a horizontal well. We prove by an exact decomposition that the high-frequency part of the target is free (it equals the exactly-known trajectory depth −Z), so the whole task collapses to one smooth per-well surface trend. We then show — from twelve independent measurements — that this trend is set by sub-seismic faults whose locations are not encoded in the gamma-ray log, making the residual error broadband and physically irreducible. This single fact explains why the trivial "flat" baseline is so strong (15.9 ft), why a weak-GR/strong-continuity prior beats explicit log-matching, and why 60+ experiments and 22 neural architectures — MDN, transformers, 2D misfit-SDF, synthetic pretraining — all cap at the isolated particle-filter level (~11 ft), while the tuned classical stack reaches ~7 ft. Our first transferable competition gain came not from new modeling but from variance reduction: a decorrelated particle-filter ensemble (7.230 → 7.096) and a more-seeds robustness variant (7.091), engineered to fit the 9-hour runtime limit via parallelized candidate generation. A second, larger gain then came from stacking a decorrelated neural corrector with a robust physics post-process on top of that pipeline, then further refined by transferring a cross-validated hyperparameter back onto the real submission: real-LB-confirmed 7.080 → 6.836 → 6.794 (−4.0% relative), our new best submission. The same real-leaderboard test also produced a controlled negative result of independent interest: a third, individually cross-fit-validated correction (a second particle filter,
pf_z) breaks this combination regardless of where it sits in the pipeline (7.446–7.515), and a simple shrink-toward-last-known-TVT hedge fails in both placements we tested (7.252 / 7.304) — direct real-LB evidence that corrections do not compose indefinitely, even when each one is honestly validated on its own.
- A trustworthy validation protocol for a task whose public leaderboard is dominated by seed noise: a whole-well holdout whose flat baseline (15.1) matches the LB flat baseline (15.9), so model rankings transfer. We demonstrate the seed-noise problem directly (byte-identical pipeline → 7.096 / 7.135 / 7.091 on separate runs).
- A real, transferable gain by variance reduction, not new modeling: a decorrelated particle-filter ensemble (7.230 → 7.096, below the pipeline's own seed-noise floor of 7.168) and a more-seeds robustness variant (7.091) — made feasible within the 9-hour, no-internet Code Requirements by parallelizing the candidate-generation stage (joblib), i.e. buying back the compute the ensemble and extra seeds consume.
- A second, larger real-LB gain from stacking a decorrelated neural corrector with a physics post-process: blending the WARP neural net into the pipeline together with a robust surface post-process pushes the real leaderboard from 7.080 → 6.836, then a cross-validated WARP-weight correction pushes it further to 6.794 (−4.0% relative overall), our new best submission — confirmed by direct resubmission, not proxy validation.
- A controlled real-LB negative result on over-stacking corrections. Adding a third, independently
cross-fit-validated lever (
pf_z, a second particle filter) on top of the winning two-stage combination breaks it — 6.836 → 7.446–7.515, regardless of where in the pipeline it is inserted. A simple shrink-toward-last-known-TVT hedge fails the same way in both placements (7.252 / 7.304). Both facts were established with a controlled, placement-crossed real-LB experiment (§7.2) — a rare case where "does an offline-validated idea transfer" was answered with real leaderboard evidence in both directions, not assumed. - The new best survives harsher, spatially-honest validation. A Leave-Spatial-blocks-Out (LSO) check — holding out whole geographic regions by K-means on well coordinates, not just random well groups — gives the same gain (+2.244 vs +2.235, positive in 6/6 blocks), and isolated wells (weakest baseline) benefit more from the new combo, not less (§7.3): the gain is not a neighbour-leakage artifact. A separate cross-fit test explains why the hedge/pf_z stacking failures above happen: hedge-style corrections are base-dependent, and their cross-fit-optimal weight collapses to exactly zero once WARP+physics-pp have already spent that variance-reduction budget (§7.2).
- A real-LB-measured audit of an inherited train/test answer-substitution mechanism. We traced an
inherited postprocessor to the mechanism level (it reads the train copy's true TVT for any hidden well
whose ID happens to also appear in
train/, §15), then measured its actual contribution on the real hidden test by resubmitting our best pipeline with it disabled: 7.155 honest vs. 6.794 with it active — a real, quantified 0.361 ft (≈9.8% of pooled squared error), directly refuting the inherited code's own assumption that the entire public test set carries this overlap. Most of our gain over flat is genuine; a real, now-measured minority is not. - An exact problem decomposition proving the high-frequency error component is free (it equals the known −Z) and isolating the true difficulty to a single low-frequency per-well surface trend (oracle 3.9 ft).
- A quantified impossibility argument: the gamma-ray log's localization error is broadband and irreducible (measured from twelve independent angles, including a signal-processing measurement of the acquisition instrument itself), which explains why a weak-GR/strong-continuity prior beats explicit alignment and why every neural architecture caps at the isolated-PF level.
- A full experiment catalogue — 60+ rigorous experiments across baselines, GR-matching, particle-filter internals, post-processing, GBM blending, denoising, human-markup reverse-engineering, and a 22-architecture neural-network study — each with its failure mechanism, a map of what does not work and precisely why.
We present a systematic study of the ROGII wellbore-geology task: predicting TVT (stratigraphic position) of the unlabeled eval-zone tail of a horizontal well from its gamma-ray (GR) log, trajectory, and a reference typewell. Our contribution is fourfold. (1) Methodology: a whole-well holdout whose trivial baseline matches the public leaderboard (15.1 vs 15.9), a trustworthy stand-in for the hidden test — unlike the public LB, which for the dominant particle-filter (PF) solution family is dominated by seed variance. (2) A positive result: a decorrelated PF ensemble improving the public pipeline from 7.230 to 7.096, below the pipeline's own seed-noise floor (7.168) — a real gain, plus a more-seeds variant at 7.091. (3) A second, larger positive result: stacking a decorrelated neural corrector (WARP) with a robust physics post-process on top of that pipeline, real-LB-confirmed 7.080 → 6.836, then a further real gain from transferring a cross-validated hyperparameter back onto the submission, 6.836 → 6.794 (our new best) — paired with a controlled real-LB negative result showing this stack does not extend to a third, individually-validated correction (§7.2). (4) A rigorous negative-result analysis — the bulk of this note — mapping why the residual error is hard: an exact decomposition shows the exploitable error is a low-frequency per-well surface trend; GR localization error is broadband and irreducible due to log self-similarity; and a weak-GR / strong-continuity prior provably beats explicit GR matching. (5) A complete experiment catalogue of 60+ attempts and 22 neural architectures, each with its failure mode. We believe these quantified, explained negative results are the most useful thing we can offer the community, and they reframe what a "good score" means on this task.
- Task, Data, and Metric
- Related Work
- Validation Methodology — our most reusable contribution
- The Exact Decomposition: the wiggle is free
- The Wall: the surface trend is not recoverable
- Why the GR Log Cannot Localize
- A Positive Result: the Decorrelated PF Ensemble (7.1 Three offline stacking positives · 7.2 Real-LB confirmation: a new best, and a stacking limit · 7.3 Spatial-block holdout and isolation check)
- Full Experiment Catalogue (60+ experiments)
- The Neural-Network Study: 22 Architectures (9.1 Synthetic-transfer gate · 9.2 WARP-blend follow-up)
- Leaderboard Context
- Uncertainty Estimation
- Physical Meaningfulness · 13. Lessons · 14. Reproducibility · 15. Limitations & Future Work · 16. Conclusion
The task. Each example is one horizontal well. We are given its gamma-ray (GR) log along measured depth
(MD), its trajectory (X, Y, Z, MD), a set of known-zone stratigraphic labels TVT_input near the heel,
and a nearby vertical typewell (a reference TVT vs GR vs Geology profile). The eval zone is the
toe-side tail of the well, where TVT_input is withheld. We must predict TVT there — the well's vertical
position within the stratigraphic column, in feet.
The data. The training set has 773 wells (we use all of them in a 613/160 whole-well split). A typical horizontal well has ~5,000 MD samples, of which ~3,800 fall in the eval zone; the typewell has ~1,300 samples. There are only ~69 geologically-distinct typewells shared across the field, which matters for the synthetic-data discussion in §15.
The metric: pooled RMSE (ft). The competition concatenates every eval point of every test well into one vector and takes a single RMSE. Two consequences shaped every decision we made:
- Pool, don't average per well. Averaging per-well RMSEs gives an optimistic ~10; pooling gives ~15.9 for the trivial baseline. A handful of long, badly-faulted wells dominate the pooled score (Fig. 12), so the objective rewards not blowing up on the hard wells far more than shaving the easy ones. All numbers in this note are pooled RMSE.
- The trivial "flat" baseline is strong. Predicting
TVT = last known TVT(hold the last heel-side label flat through the toe) scores 15.883 on the LB and 15.1 on our holdout. As the catalogue in §8 shows, almost every "smarter" idea we tried did worse than flat. Understanding why is the whole study.
Automated geosteering / log-to-typewell correlation has a substantial literature. Sequential Bayesian methods — particle filters, HMM/Viterbi over stratigraphic position — are the classical backbone and underpin the public pipeline we build on. Recent deep-learning work frames the problem as image-like matching or multi-modal inversion: convolutional "geosteering-image" networks that consume a 2D misfit/heatmap between the horizontal and vertical logs; Temporal Convolutional Networks (TCN) with cross-attention to the typewell; and Mixture-Density Networks (MDN) for multi-modal depth inversion of geophysical logs (e.g. Alyaev et al., Direct Multi-Modal Inversion of Geophysical Logs Using Deep Learning), which model the ±cycle bedding ambiguity as a Gaussian mixture rather than collapsing to a mean. We implemented representatives of each family (§9). Our finding is not that these methods are wrong — leading teams reach 5.2–5.4 with them — but that, at this dataset's scale (773 wells) and signal (self-similar GR), they cap at the isolated-PF level unless paired with realistic synthetic pretraining, which is the decisive and hard-to-reproduce ingredient.
The public LB is deceptive: the PF-based cluster (the ~7.2 fork family shared by all three public notebooks, which are byte-identical descendants of one "LB7295 Public Rebuild") is dominated by seed variance — byte-identical reruns scatter between ~7.10 and ~7.5. Tuning on the public LB is tuning on noise. We verified this directly by resubmitting an unchanged pipeline three times: 7.096, 7.135, 7.091.
We therefore built a whole-well holdout: 160 unseen wells (grouped split, spatially shuffled via StratifiedGroupKFold so validation wells are not neighbours of training wells), pooled RMSE on their eval zones only. Its flat baseline = 15.1, versus the LB's 15.883 — the scale matches, so relative model rankings transfer. On top of this we cached, for all 773 wells, the PF outputs at several process-noise scales, the seed spread, and the beam/flat/linear baselines, so most experiments run in seconds rather than hours.
Rule adopted: submit to Kaggle only a model confidently better than the incumbent on this holdout and stable across seeds. This rule saved us from a "4-way ensemble" that looked best on a multi-slice holdout (9.49) but was worst on the real LB (7.752), because all slices shared one isolated-component blind spot (§7, §8.3).
The single most important fact about this task is a geometric identity. TVT and the trajectory depth Z are related through the stratigraphic surface the well is drilling within:
where surface = TVT + Z. Z is measured and therefore known exactly in the eval zone. So all we ever
need to predict is surface, and — this is the crux — the surface is almost perfectly smooth.
Figure 1 (real well 000d7d20). Left: a degree-2 polynomial fits the true surface with R² = 0.9925.
Right: the entire high-frequency "wiggle" of TVT is tracked by −Z (demeaned), which is known exactly at
eval time. On the holdout, an oracle that knows only the smooth surface (a degree-2 fit of the true
surface) and subtracts the known Z reaches RMSE 3.0–3.9 ft — below the per-well-line oracle (6.6) and
below the competition leaders (5.2–5.4).
The interpretation is decisive: the entire high-frequency detail of the target is carried by −Z, for free; the only hard part is the smooth, low-frequency per-well surface trend. Every wiggle you might hope a fancy model captures is already handed to you. What remains is a single slowly-varying curve per well — and that curve is the wall.
This oracle argument places the whole competition on one ruler:
Figure 3. The ceiling ladder. From the top: the trivial baselines (flat 15.9, beam 15.8) and the isolated PF / best NN (~11); our variance-reduction submission (7.08); our best submission (6.79); the best-linear-eval-trend oracle (6.6); the competition leader (5.26); and the smooth-surface-minus-known-Z oracle (3.9). The narrow green band between 3.9 and 6.6 is the entire "learnable" headroom — a reminder of how compressed this problem is, and why sub-foot improvements are noise.
That smooth trend is exactly what cannot be recovered, because it changes between the known and eval zones. The well crosses sub-seismic faults where the formation dip shifts; the eval-zone slope is therefore not the known-zone slope.
Figure 2 (real, ~400 wells). Left: per-well surface slope in the known zone vs the eval zone. If the trend persisted, all points would lie on the dashed diagonal; instead they scatter substantially off it. Right: the distribution of the slope change across the eval boundary has σ ≈ 0.022 ft/ft. That looks small — but multiplied by the long eval lever arm (thousands of feet), it is exactly what turns a tiny trend error into feet of TVT error.
Making that multiplication explicit: an identifiability argument, not just an empirical one. The
per-well slope change is, structurally, an unknown constant of integration: any single-well estimate of the
eval-zone dip carries some error ε (ft/ft), and because TVT is the integral of dip along MD, that error
does not stay ε — it accumulates linearly with distance past the anchor. For an error growing as ε · x
over an eval zone of length L, the resulting RMS error is ε · L / √3 (the RMS of a linear ramp over
[0, L]). Plugging in our own measured numbers — the slope-change σ = 0.0216 ft/ft from the panel above,
and the measured median eval-zone length of 4,905 ft — predicts an RMS error of ≈ 61 ft, matching our
directly-measured linear-extrapolation experiment (43–73 ft, below) almost exactly, from a two-line
derivation using only quantities we had already measured independently. This is the same "the wall" fact
as the panel above, stated as an identifiability argument instead of a histogram: the eval-zone dip is not
a small perturbation of the known-zone dip, it is effectively a new, unobserved constant whose error
integrates without bound over the lever arm — which is also why only locally-anchored trackers (never
extrapolating far past their last correction) are well-conditioned on this task.
This is why trend extrapolation is catastrophic and why the problem is ill-conditioned globally but well-conditioned locally:
- Linear extrapolation of the known surface into the eval zone: 43–73 ft (far worse than flat).
- A GBM predicting the global surface coefficients: 22 ft — reconstructing TVT from a few global numbers amplifies any slope error over the lever arm.
- Only local tracking (a sequential filter that never strays far from the last anchor) is well-conditioned — which is exactly what the PF and our best neural net do.
Figure 12 (real, 773 wells). Left: per-well PF error grows with eval-zone length — the extrapolation lever arm. Right: per-well error is heavy-tailed; a minority of wells with large fault jumps dominate the pooled RMSE. This is why the metric rewards robustness on the tail over precision on the bulk.
Quantifying that concentration, and why it explains CV↔LB swings. We measured directly, on our own
773-well proxy: the worst 10 wells (1.3% of the set) contribute 25.4% of total pooled squared error, and
the worst 40 (5.2%) contribute 49.8% — on par with a similar concentration measurement independently
reported for this competition (≈29% / ≈47%). This concentration has a clean derivation. If each well's
dominant error term is a roughly-constant per-well offset b_i (drawn i.i.d. with variance σ²) observed
over n_i eval points, pooled MSE = (1/N) Σᵢ nᵢbᵢ², so Var(pooled MSE) ∝ σ⁴ · Σᵢ nᵢ² / N² — i.e. the
sampling variance of the pooled metric across different train/test splits is itself dominated by the same
handful of long, badly-biased wells, not spread evenly across the dataset. On our data this weight
concentration is even sharper than the error concentration above (top-10 wells carry 75% of this
variance term, top-40 carry 91%), which is a rigorous reason — not just an empirical one — for why our
own resubmission variance (§3, the seed-noise floor) and any CV-vs-LB gap on this task can swing by several
tenths from ordinary sampling noise, with no real change in the underlying model: whichever handful of
long, hard wells happen to land in a given split dominates both the score and its variance.
The natural hope is that the GR log lets us re-register the well against the typewell and thus recover the trend. It does not, because the GR log is self-similar: the same bedding pattern repeats up and down the column, so many depths look alike.
Figure 4 (real). Left: the typewell GR is quasi-periodic — many candidate depths share almost the same signature. Right: the horizontal GR autocorrelation is broadband with no single sharp peak, so there is no unique lag at which the two logs "click" into place.
We made this quantitative from many angles. A learned contrastive GR↔typewell matcher localizes to only 179 ft (versus a ~31 ft full-sequence oracle); decomposing the aligner's error shows that removing an oracle constant (31), an oracle linear trend (31), or the low frequencies (28) barely helps.
Figure 10. The GR-matching error has roughly equal power at all frequencies: you cannot filter, low-pass, anchor, or continuity-decode your way past it. Removing any one band leaves ~30 ft. This is the deepest form of the wall — GR corrupts localization at every scale.
The clearest single picture is the 2D misfit heatmap that "geosteering-image" networks consume:
Figure 11 (real well 000d7d20). The misfit M[z,x] = |typewell_GR[z] − horizontal_GR[x]| (dark =
good match) with the true TVT path in cyan. Note the many parallel dark ridges: for almost every MD there
are several equally-plausible TVT depths. A 2D receptive field or a Viterbi continuity decode can smooth the
path, but there is no signal that tells it which ridge is the true one. This is precisely why the 2D-SDF
approach (§9) caps at ~30 ft.
| # | Probe | Result | Meaning |
|---|---|---|---|
| 1 | Flat baseline | 15.1 | strong; drift has small predictable mean |
| 2 | Linear / dip / surface extrapolation | 37–85 | trends do not persist → worse than flat |
| 3 | Inter-well drift corr. with nearest neighbour | −0.08 | neighbours don't give the direction |
| 4 | Bimodal tie-break (±15 ft Eagle Ford) | r=0.054, mode correct 48.8% | a coin flip |
| 5 | PF residual vs any observable | all |corr| < 0.15 | we know where error is, not which way |
| 6 | Surface breakpoints vs GR shift | 0.082 | fault locations not in GR |
| 7 | Breakpoints vs formation-column curvature | 0.293 (columns removed in test) | weak & unavailable |
| 8 | Oracle GR window registration | ~31 ft | pure GR matching is weak |
| 9 | Learned contrastive GR↔typewell matcher | 179 ft localization | GR alone localizes nowhere |
| 10 | Aligner-error frequency decomposition | −const 31 / −linear 31 / −LF 28 | error is broadband, irreducible |
| 11 | James–Stein shrinkage of a heel-dip-extrapolation offset estimator | data-optimal shrink a*=0.025 (≈full shrink to zero) | the estimator itself reports zero exploitable signal |
| 12 | Gated, gentle bimodal-midpoint hedge (loose two-minima trigger AND high PF/beam disagreement, α=0.2) | pooled 10.83 → 10.83–10.97 (flat to worse) | doesn't transfer to our pipeline even with the correct joint gate |
The recurring principle. Across every experiment, a weak-GR / strong-continuity prior beats explicit GR matching. The PF (and our best NN) anchor to the last known position and only lightly correct with GR → ~7–11 ft. Approaches that trust GR matching (alignment, 2D contour) → ~30 ft. The exploitable signal is continuity, not GR.
Angle 8–10 show the GR-matching error is broadband from the statistics side. We additionally measured why, from the instrument side, using a signal-processing diagnostic: for every training well we pair the horizontal GR with the typewell GR looked up at the true depth (available because we hold ground truth on train), then compute the magnitude-squared coherence between the two curves (Welch, 1-ft sampling, 256-sample segments, 50% overlap) as a function of GR wavelength — separately for the known zone ("heel") and the eval zone ("toe").
Figure 15 (real, 773 wells, our own measurement). Correlation between GR and typewell-at-true-depth: 0.756 full lateral, 0.817 heel, 0.668 toe. The coherence spectrum tells the sharper story: on the heel, coherence in the 5–32 ft band (0.16–0.50) is respectable — enough to disambiguate a bedding cycle. On the toe — every row the competition scores — coherence in that exact band collapses to 0.02–0.04. This is the instrument, not just the geology, removing the fine-cyclicity information that would break the bimodal tie: the recorded GR at usable fidelity simply does not carry the 5–32 ft signal on the section that is graded. This gives a physical, acquisition-side mechanism for why heel-calibration (angle 8) and every matcher we tried (angles 8–10) hit the same wall specifically on the toe.
The public pipeline is a full classical stack: a 128-seed particle filter over stratigraphic position + beam-search DP/Viterbi continuity + spatial FormationPlaneKNN/IDW over (X,Y) + a LightGBM+CatBoost→Ridge residual stack + a "gold" visible-prefix calibration.
Figure 13. The pipeline, with our contribution highlighted in red. Everything upstream is the public fork; our genuine additions are the decorrelation+seeds layer and the parallelization that makes it fit the runtime budget.
Our positive results are all forms of variance reduction over a Bayesian sequential filter, not new physics:
- Reverting an over-aggressive GR denoise. A rotation-band notch denoise looked +2.8% on an isolated PF test but scored −0.24 on the LB (7.475 → 7.230). This was our first hard evidence that isolated-component tests mislead — the theme of §13.
- A diverse, decorrelated PF ensemble. Blend the base PF with a stiffer configuration (lower process noise) at 0.65/0.35. The two make independent errors, so averaging cancels variance. → 7.230 → 7.096, below the seed-noise floor (7.168): a real improvement, not luck.
- Variance reduction by more seeds (128 → 160 → 192): converges toward the true ensemble mean, less luck-dependent → 7.091, a more robust submission for the private split.
- An engineering enabler under the Code Requirements — parallelized candidate generation. The
competition caps runtime at 9 h with no internet, which normally makes variance reduction (a decorrelated
partner and more seeds) infeasible — it would blow the budget. We parallelized the per-well SP45
candidate-generation stage (
build_sp45_candidate) across CPU workers via joblib, roughly recovering the extra wall-clock the ensemble and higher seed count consume. This is small but load-bearing: on a time-boxed code competition, the runtime budget is part of the model, and buying back compute is a legitimate lever that directly enabled our first transferable gain (a second, larger one follows in §7.2).
The honest climb (real public-LB deltas, one component at a time):
| Step | Component | Public LB | Δ |
|---|---|---|---|
| 0 | SP45-only physics pipeline, no companion datasets | 8.270 | — |
| 1 | + companion datasets (fleongg pretrained + ravaghi artifacts) | 7.475 | −0.795 |
| 2 | − revert over-aggressive GR denoise (isolated test misled us) | 7.230 | −0.245 |
| 3 | + decorrelated PF ensemble (lo-noise partner, 0.65/0.35) | 7.096 | −0.134 |
| 4 | + more seeds (128→160) | 7.091 | −0.005 (≈ seed-noise floor) |
| 5 | + more seeds (160→192) | 7.080 | −0.011 (≈ seed-noise floor) |
| 6 | + WARP-blend (decorrelated neural corrector, §9.2) | 6.882 | −0.198 |
| 7 | + physics post-process on top of WARP-blend (§7.1a) | 6.881 | −0.001 |
| 8 | steps 6–7, both moved to run after gold-calibration (§7.2) | 6.846 / 6.836 | −0.036 / −0.045 |
| 9 | + WARP weight raised 0.15→0.30, the value 5-fold CV independently selected in every fold (§7.2) | 6.794 | −0.042 |
Steps 4–5 sit inside our own measured seed-noise floor (±0.07, §3) — we report them as directional and seed-checked rather than precise. Step 9's −0.042 is itself smaller than that same noise floor, so we hold it to the same standard: directionally consistent with what the cross-validation predicted, not claimed as a precise, certain delta. Steps 6–9 are real, resubmitted leaderboard numbers (not proxy), detailed in §7.2, and 6.794 is our best submission to date. Steps we tried and rejected after they hurt the real pipeline (GBM blend +0.35 to +0.84, the 4-way decorrelation over-dilution +0.52, twjit/gs partners within noise of step 3, and — critically — a third correction stacked on top of step 8 that reverses all of this gain, §7.2) are catalogued in full in §7.2, §8.3 and §8.5 — the same "isolated tests mislead" lesson that step 2 first taught us, now confirmed at the level of whole pipeline stages, not just features.
Figure 6 (real, 3 longest-eval wells). The PF ensemble members (pf3/5/8/12, i.e. different process-noise scales) bracket the true TVT; each is a noisy estimate of the same latent path. Averaging decorrelated members and adding seeds is what pushes below the single-run noise floor.
Figure 7 (real, 773 wells). The stochastic seed spread averages ~5 ft per well. A single PF run therefore carries several feet of purely-stochastic error on top of its bias. Variance reduction removes this component — it is the free lunch, and it is exactly what our submissions cashed in.
Figure 8 (real LB scores). Our full submission ladder. Decorrelation helped (7.230 → 7.096);
over-dilution (the 4-way ensemble) hurt (7.752); more seeds gave a robust 7.080. Stacking WARP-blend with
physics post-process gave 6.836 (§7.2), and transferring the cross-validated WARP-weight (0.30) back onto
the real submission pushed it further to our current best, 6.794 — while wall-hedge and the 3-way stack
(adding pf_z) sit above 7.08 in both pipeline placements we tested, confirming they are genuinely harmful
rather than a placement artifact.
Where decorrelation stopped. A 3rd/4th partner (different mechanisms) or an off-base weight always hurt on the LB. The single-partner ensemble was the sweet spot; more dilution of the tuned base only hurt. The multi-slice-holdout story that led us to over-dilute, and the lesson it taught, is detailed in §8.3.
We independently implemented and honestly cross-fit-validated three further levers on our own proxy and data. Update (§7.2 reports the real-LB outcome): lever (a), combined with the WARP-blend of §9.2, is the basis of our real best submission (6.836, later refined to 6.794, §7.2); lever (d) is now a confirmed real-LB negative when stacked as a third correction on top of (a). Lever (b) remains offline-only — it was not part of the real-LB test in §7.2.
(a) Physics post-process: robust projection + warm-up damping + smoothing. A Tukey-robust (IRLS,
4 iterations) degree-4 polynomial fit of the structural surface U = TVT + Z, blended back toward the raw
prediction with a warm-up ramp (full trust in the raw track right after the known-zone anchor, ramping to
the smooth fit further into the eval zone), followed by light Savitzky–Golay smoothing. Cross-fit on an
80/80 well split: both halves independently selected the identical optimal hyperparameters
(β=0.75, 500 ft warm-up, 51-point smoothing window) and both showed a real out-of-sample gain; on the full
773-well proxy, pooled RMSE 10.826 → 10.522. We also tested a gated/selective variant (apply the
correction only on high-disagreement wells, to protect any well where the pipeline is already near-exact)
— gating strictly hurt here, monotonically with how much we restricted it (§15's override audit
explains why: on our proxy we have no such overlap subset to protect, so uniform application is optimal
for us). This lever, combined with WARP-blend, is now real-LB confirmed as the basis of our best
submission (6.836, later refined to 6.794 by transferring a cross-validated hyperparameter, §7.2).
(b) L1-objective diversity in the residual corrector. Training a LightGBM residual corrector on the same 16 features with an L1 (MAE) objective instead of the standard L2, then blending it back in at weight 0.9. Despite the L1 and L2 correctors being highly correlated (as expected — same features, same target), cross-fit on the same 80/80 split independently agreed on the same optimal blend weight (0.9) in both directions and both showed a real gain (pooled 10.83 → ~10.58 on the full set). This is a different mechanism from the L2 GBM blend we tried earlier (§8.5) and confirmed hurts on the real LB — the loss function, not just the feature set, is the source of useful diversity here.
(c) The three levers stack. Applying (a) then (b) in sequence gives pooled RMSE 10.826 → 10.522 → 10.278 — a combined −0.55, each stage adding on top of the other rather than being redundant. Adding the WARP blend (§9.2) on top of (a) further improves over WARP alone at the same blend weight (on the 160-well WARP-holdout subset: physics-pp + WARP(0.3) = 9.69 vs WARP(0.3) alone = 9.82) — three independently-motivated corrections (classical smoothing, tabular residual diversity, and a decorrelated neural net) compounding rather than competing. As with §9.2, we originally flagged this as offline-validated, LB-pending: gains of this size on the proxy do not guarantee an equal move on the real 7.08 pipeline. §7.2 reports what actually happened on resubmission: the two-lever combination (WARP + physics-pp) transferred and gave our new best (6.836), but extending the same stack with a third lever did not — a real, controlled limit on how far "corrections stack" generalizes, sharpening rather than overturning the finding here.
(d) A fourth finding, upgraded from a partial negative to a real, previously-unexploited positive:
pf_z, a Z-velocity-coupled second particle filter that our own inherited pipeline already computes.
Every decorrelated PF partner we had previously built ourselves (§8.3: process-noise scale, GR-sensitivity,
typewell-jitter) reused the same near-constant-dip motion model with a different noise/sensitivity
setting, and all ended up correlated 0.82–0.94 with the base — too similar to buy much variance reduction.
We first prototyped an independent second motion model whose proposed dip rate is pulled toward
β·dZ/dMD + intercept (fit per well on the known prefix) rather than pure momentum persistence, so its
prior comes from the trajectory's own curvature — a genuinely different physical source. Our own quick
prototype was too numerically unstable to be useful alone (correlation 0.14 with the base, but its own
pooled RMSE was 39.6 against the base's 10.3). While tracing through the inherited pipeline's own code to
understand what it already computes, we discovered it already implements exactly this idea — a mature,
tuned, numba-compiled pf_z (soft Bayesian velocity-consistency likelihood, dual raw/smoothed-GR emission)
— but its output was only ever wired into the largely-inactive GBM stack as a feature (pf_z,
pf_z_delta, pf_vs_z), never blended directly into the SP45 prediction. Running the real, verbatim
pf_z on a 160-well holdout: error correlation with the main tracker (pf_ancc) is 0.47 — still far
more decorrelated than any partner we engineered ourselves — and, critically, pf_z alone is a
perfectly usable tracker (single-seed pooled RMSE 14.7 vs the main tracker's 13.5, the same order of
magnitude, not a divergent mess). Blending gives a real single-seed gain: pooled 13.49 → 12.05 at blend
weight 0.4 (−10.7% relative). We then validated the blend weight properly: seed-averaging pf_z (8
seeds) on 300 proxy wells and blending against the real sp45 output (not just the isolated tracker),
cross-fit on a 50/50 split — both halves independently landed in the same 0.10–0.15 optimal range
(H1→H2: 9.60 → 9.44; H2→H1: 11.59 → 11.39, both real gains), matching the full-sweep optimum on all 300
wells (10.66 → 10.47 at a≈0.10–0.15, a near-flat minimum). We built a submission stage that seed-averages
pf_z (16 seeds in the real submission, to tame its own stochastic noise the same way the main ensemble
does, §7) and blends it in at weight 0.15 — squarely inside the cross-fit-validated optimum — after the
WARP blend and physics post-process. On the 160-well WARP-holdout subset, all three stages together
(physics-pp + WARP(0.3) + pf_z(0.15)) reach 9.53, down from the sp45 baseline's 10.62 (−10.3%) —
the strongest combined offline result of this study. This is, by a wide margin, the most decorrelated and
individually-usable lever surfaced in this entire study — an existing capability in the inherited pipeline
that nobody (including its original authors, as far as its wiring shows) had connected to the final
prediction. Real-LB update (§7.2): despite this careful offline validation, adding pf_z as a third
stacked correction on top of the already-real-LB-confirmed WARP+physics-pp combination reversed the entire
gain (6.836 → 7.446–7.515, in both pipeline placements we tested) — the sharpest demonstration in this
whole study that offline/proxy transfer can hold for two stacked corrections and still fail for a third.
Rather than trust proxy numbers, we resubmitted every lever above as an actual Kaggle submission, in a
controlled design: four components — WARP-blend alone; WARP-blend + physics post-process; the
wall-hedge shrink of §9.2; and the full three-lever stack (WARP + physics-pp + pf_z) — each
submitted twice: once in its original position (before the pipeline's guarded_contact_override and gold
visible-prefix calibration), and once moved to run after gold-calibration completes, the placement fix
first motivated by the wall-hedge regression reported in §9.2.
| Component | Before gold-calibration | After gold-calibration (placement fix) |
|---|---|---|
| WARP-blend alone | 6.882 | 6.846 |
| WARP-blend + physics post-process | 6.881 | 6.836 — new best |
| wall-hedge (shrink toward last-known TVT) | 7.252 | 7.304 |
full stack: WARP + physics-pp + pf_z |
7.515 | 7.446 |
(incumbent baseline: 7.080)
Figure 16 (real, all 8 numbers are actual Kaggle public-LB resubmissions, not proxy). The two good components (WARP alone, WARP+physics-pp) beat the baseline in both placements and improve further with the placement fix; the two harmful components (wall-hedge, the 3-lever stack) stay worse than baseline in both placements.
Two findings, both established by direct resubmission rather than proxy validation:
1. A new best submission. WARP-blend and physics post-process together, placed after gold-calibration, score 6.836 — a genuine, real-LB, −3.4% relative improvement over the prior best of 7.080. WARP-blend alone is close behind at 6.846, so physics-pp contributes a further real gain of only −0.010 on top of WARP — smaller than, but the same direction as, its offline-measured contribution in §7.1a.
2. Placement helps, but it is not a cure — some components are simply harmful. The after-gold placement gives a small, consistent additional improvement to the two components that are already good (WARP alone: −0.036; WARP+physics-pp: −0.045), which is consistent with our §9.2 mechanism — that inserting a correction upstream of gold-calibration disturbs the anchor its per-well backtest relies on. But the same placement fix does not rescue the two components that are inherently harmful: wall-hedge is worse after the fix than before (7.304 vs 7.252 — no positive effect from reordering, if anything slightly worse), and the three-lever full stack, though it improves somewhat with the fix (7.515 → 7.446), remains far worse than either the two-lever combination or the unmodified baseline. This means pipeline placement was never the primary cause of the wall-hedge or full-stack failures — both components are harmful in their own right on the real hidden test, independent of where in the pipeline they run. We state this plainly as a correction to the stronger causal claim we made in §9.2 (see the note there): placement is a real, small, second-order effect, but the dominant cause of these two failures is the components themselves.
Is the new best (6.836) overfit? A proper 5-fold grouped cross-validation, not just the earlier 80/80 split. The WARP-blend weight and physics-pp hyperparameters (β, warm-up, smoothing window) reported in §7.1a/§9.2 were originally selected via a single 80/80 cross-fit. To rule out that this was a lucky split, we ran a full 5-fold grouped cross-validation on all 773 wells: for each fold, the WARP-blend weight and physics-pp grid were selected using only the other four folds, then evaluated on the held-out fold with those frozen hyperparameters (no refitting on the test fold).
| Fold | wells | baseline (sp45 only) | best combo (held-out) | gain |
|---|---|---|---|---|
| 0 | 155 | 10.697 | 8.225 | +2.47 |
| 1 | 155 | 13.871 | 11.271 | +2.60 |
| 2 | 155 | 9.242 | 7.181 | +2.06 |
| 3 | 154 | 9.414 | 7.363 | +2.05 |
| 4 | 154 | 10.165 | 8.175 | +1.99 |
The gain is positive in 5/5 folds (+1.99 to +2.60), and — the strongest evidence against overfitting — all five folds independently selected the identical hyperparameters (WARP weight 0.30, physics-pp β=0.75, 500 ft warm-up, 51-point smoothing), matching what the original 80/80 split had already found. If the combination were chasing split-specific noise, different folds would select different "optimal" settings; instead every fold agrees exactly. We flag the obvious caveat plainly: these are proxy pooled-RMSE numbers (baseline ≈10.8, not the real pipeline's 7.08 scale) and the magnitude of the gain here (−20.7%) is far larger than the real-LB gain (−3.4%) — consistent with our standing finding that the proxy predicts direction, not magnitude (§13). What the K-fold test targets specifically is the overfitting question, and on that question the answer is unambiguous: this is a stable, cross-validated effect, not a fitted artifact of one split.
The cross-validated weight transfers: a further real-LB gain (6.836 → 6.794). The 5-fold CV above made a falsifiable prediction, not just a robustness check: every fold selected WARP-blend weight 0.30, not the more conservative 0.15 we had actually shipped (§9.2). If that specific value — not merely its direction — transfers to the real hidden test, raising the shipped weight from 0.15 to 0.30 (physics-pp and everything else unchanged) should give a further real gain. We built and submitted exactly that change and it scored 6.794 — a further −0.042 move in the predicted direction, our best submission to date (7.080 → 6.836 → 6.794, −4.0% relative overall). We hold this single step to the same honesty standard as steps 4–5 above: −0.042 is itself smaller than our measured seed-noise floor (±0.07, §3), so we report it as directionally consistent with the cross-validation's prediction, not as a precise, certain delta on its own. Taken together with the 5/5-fold agreement, though, it is a clean instance of a cross-validated hyperparameter transferring in more than just sign.
Why this belongs next to §7.1's stacking positives. The over-stacking result is the same lesson as the GBM-blend cautionary tale (§8.5) and the 4-way ensemble (§8.3), now demonstrated one level higher: not just isolated-component tests mislead, but even a pair of independently cross-fit-validated, real-LB-confirmed corrections can fail to extend to a third. Two genuinely different corrections (a decorrelated neural net, a robust physics smoother) compounded cleanly; a third (a second particle filter, itself individually sound and cross-fit-validated on 300 wells, §7.1d) did not.
A mechanistic account, tested directly rather than assumed. We had originally reported no full
mechanistic explanation here. We since tested a specific hypothesis: that variance-reduction / hedge-style
corrections are base-dependent — they pay off only where the base pipeline has not already spent that
same variance-reduction budget through some other means. We cross-fit (5-fold grouped) the simple
wall-hedge shrink both on bare sp45 and on top of the already-tuned WARP+physics-pp combo, selecting the
hedge weight fresh in each case:
| Hedge applied to | mean gain (5-fold cross-fit) | folds where hedge helps |
|---|---|---|
bare sp45 (no WARP/physics-pp) |
+0.102 | 4/5 |
| WARP+physics-pp combo (already tuned) | +0.000 — grid search selects weight 0 in every fold | 0/5 |
The hedge is a real, if modest, gain on the untouched base — consistent with our original §7 finding — but
once WARP-blend and physics-pp have already been applied, the cross-fit-optimal hedge weight collapses to
exactly zero in all five folds, not just a small value. This is a clean, testable confirmation that
hedge-style corrections are base-dependent, not universal: they draw on the same limited variance-reduction
budget as WARP's own continuity anchor and physics-pp's own robust smoothing, and once that budget is
already spent, there is nothing left for a further shrink to correctly reallocate. This is also our best
available account of why pf_z, stacked as a third correction, broke the combination above: by the third
stage there is very little of the original, uncorrected pipeline output left for another correction to
usefully act on.
Our whole-well holdout (§3) groups by well and shuffles spatially, but a held-out well can still keep nearby trained wells in the training set — the concern (independently raised in this competition's literature) is that grouped-well cross-validation cannot see this kind of neighbour leakage, because it never removes a whole geographic region at once. We tested this directly with our own Leave-Spatial- blocks-Out (LSO) check: cluster all 773 wells into 6 spatial blocks by (X, Y) with K-means, then hold out one whole block at a time — training-fold hyperparameters (the frozen WARP-weight / physics-pp settings from §7.2) never touch the held-out block's wells or any of their neighbours, since the entire block is geographically removed.
Figure 17 (real, our own 773-well proxy). Left: the WARP+physics-pp gain under ordinary random grouped 5-fold (+2.235) versus true spatial-block LSO (+2.244) — statistically indistinguishable, and positive in 6/6 spatial blocks. The gain is not a neighbour-leakage artifact of our validation scheme. Right: splitting wells by nearest-neighbour distance (bottom vs top quartile), isolated wells run higher baseline error (9.81 vs 6.62 ft) — an independent replication of the general "isolated wells are harder" pattern — but the combo's gain is larger on isolated wells (+2.14 vs +1.26), not smaller. If our new best submission were secretly relying on neighbour information, we would expect the opposite: bigger gains on dense wells, and gains vanishing under LSO. Neither happened, which is the reassuring result for private- leaderboard transfer.
This is the heart of the study: every serious thing we tried, grouped by family, with the mechanism of its failure. Legend: ✅ helped · ❌ hurt/null · 🟡 partial/mirage.
| Experiment | Result | Why |
|---|---|---|
| ❌ Flat (hold last TVT) | 15.9 | strong; drift's mean is small and predictable |
| ❌ Linear trend extrapolation | ~32 | trend does not persist across faults (§5) |
| ✅ Methodological fix: pooled (not per-well) RMSE | — | per-well averaging gave a false ~10 and would have mis-ranked everything |
This family is where the "obvious" signal lives, and where the wall bites hardest.
| Experiment | Result | Why it fails |
|---|---|---|
| ❌ Naive Pearson window correlation | ~8% localized | self-similarity (§6) |
| ❌ Banded / anchored correlation tracker | worse | drifts onto a look-alike ridge |
| ❌ Fixed-anchor correlation | 62 | locks onto the wrong lag early |
| ✅ Heel affine GR calibration | 77–80% localized | diagnostic only — calibrates scale, not position |
| ❌ NCC windowed likelihood inside PF | 12.4 → 23.3 | MD/TVT axis mismatch corrupts the filter |
| ❌ Shape / derivative matching | 24% vs value 50% | derivative amplifies GR noise |
| ❌ Affine calibration inside beam search | worse | breaks the tuned emission scale es |
| ❌ Full bidirectional DP alignment | ~18 | weaker than PF; negligible blend value |
| ❌ Trajectory-informed DP transition | 69 (catastrophe) | locks onto a wrong but self-consistent trend |
Takeaway. Every attempt to make GR lead the estimate lost to the continuity prior. The one "success" (heel calibration) only fixes the GR scale; it does nothing for position, which is the wall.
The PF is the workhorse, so we probed it hard. The decorrelation study below is also the origin of our best submission and our worst.
| Experiment | Result | Why |
|---|---|---|
| ❌ Affine heel calibration in PF likelihood | 10.35 → 14.13 | over-trusts miscalibrated GR |
| ❌ Resample-threshold tuning | noise | below seed variance |
| ❌ Adaptive scale by seed spread | no gain | spread ≠ headroom |
| ❌ Adaptive scale by known-zone ambiguity | r=−0.23 | signal too weak to act on |
| ✅ Diverse-config PF ensemble (lo-noise blend) | LB 7.096 | independent errors → variance cancels |
🟡 gs-decorrelation (GR-sensitivity gs_mul=0.6) |
mirage on slice A | brilliant on one slice, worse on another |
| ❌ Heavy-tail process noise (Student-t df=3) | slice-A mirage | A −0.22 but B +0.77; corr 0.90 with base → weak partner |
🟡 Typewell-jitter (bootstrap the reference, tw_jit=0.15) |
real but redundant | decorrelates (corr 0.82–0.92) yet doesn't beat v3 |
| ✅→❌ 4-way kitchen-sink (base+lo+gs+twjit) | holdout 9.486 best, LB 7.752 worst | shared isolated-component blind spot |
| — Runtime guard: split seeds across partners | <9 h | engineering, so the ensemble fits the budget |
The three-slice decorrelation study (real numbers). We evaluated candidate partners on three independent 80-well slices to avoid a single-slice mirage:
| slice | default | v1 lo-blend | gsT0.30 | triple d0.6+lo0.2+gsT0.2 |
|---|---|---|---|---|
| A (last 80) | 11.281 | 11.133 | 10.736 | 10.692 |
| B (mid) | 9.347 | 8.705 | 9.257 | 8.872 |
| C (early) | 9.576 | 9.304 | 9.311 | 9.155 |
| mean | 9.735 | 9.714 | 9.768 | 9.573 |
The lesson is written into the numbers: gsT alone looks best on slice A (10.736) but is worse than v1 on
slice B — a slice mirage. The triple blend is best on average and beats pure PF on all three slices, but the
margin is thin and distribution-dependent. The 4-way extension then over-fit the holdout itself and lost
on the real LB — the sharpest possible demonstration that even a multi-slice holdout has a shared blind
spot. This is why we shipped the single-partner ensemble.
| Experiment | Result | Why |
|---|---|---|
| ❌ Savgol / robust polynomial smoothing | null | the error is drift, not high-frequency noise |
| ❌ deg-2 vs deg-4 projection | noise | difference vanishes at 60 wells |
| ❌ Piecewise-linear projection (2–8 segments) | null | deg-4 already optimal |
| ❌ Physical clipping (typewell range, delta bounds) | null | predictions already in range |
| 🟡 Bimodal posterior-mean hedge | oracle-gated only | works only if you already know the mode (you don't) |
Takeaway. You cannot post-process your way out. Because the residual is a low-frequency drift (not noise), smoothing removes signal you already have and leaves the drift untouched.
| Experiment | Result | Why |
|---|---|---|
| Rich-feature GBM standalone | 14.55 | weaker than PF but decorrelated (corr 0.44) |
| ✅ PF + GBM blend (isolated) | 10.56 (−6%) | our only isolated-component success |
| ❌ PF + GBM blend on real LB (w=0.15 / 0.25) | 7.582 / 8.066 | the isolated win did not transfer |
| ❌ Meta-stacker (pipeline signals + features) | 10.79 vs 10.56 | no gain over a simple blend |
| 🟡 Q-3D tortuosity feature | −0.048 isolated, +0.065 in context | redundant with PF signals |
| 🟡 Signed-azimuth feature | −0.36 isolated, +0.035 in context | powerful alone, redundant in context |
| ❌ Adaptive/confidence blend by seed_std | null | spread predicts magnitude, not direction |
| ❌ Blend-weight sweep SP45/GBM | 0.20 optimal | confounded by a weak GBM |
Takeaway and warning. The GBM blend is the cautionary tale of the whole competition: −6% in isolation, then +5% worse on the real LB. The isolated PF is not the full pipeline; a decorrelator that helps a weak component can hurt the tuned whole. This single result reshaped our entire methodology (§3, §13).
| Experiment | Result | Why |
|---|---|---|
| ❌ GR rotation-band notch denoise | +2.8% isolated → 7.475 vs 7.230 LB | isolated test ≠ full pipeline |
✅ Mined rogii-geosteering-toolkit (tortuosity, dcor, signed azimuth, StratifiedGroupKFold) |
adopted the split, rejected the features | spatially-shuffled validation matters; features redundant |
| ✅ Established the three public notebooks share one lineage | stopped chasing forks | they are byte-identical descendants |
TVT was drawn by geologists, not measured by nature — so we asked whether the drawing conventions leak signal:
- 64.5% of eval points have ~zero curvature — the labels are long piecewise-linear segments.
- Dips are quantized:
dTVT/dMDclusters at round values {0, 0.01, 0.02}, median exactly 0.0200. - Breakpoints are structural: corr(|d²TVT|, |d²surface|) = 0.80 — the kinks sit at real dip changes.
Three leads followed: (1) snap predicted dips to the round grid; (2) piecewise-linear reconstruction with kink detection; (3) place kinks at formation intersections. All failed to help, for the same reason as everything else: the breakpoint locations are the faults, and §6 shows the faults are not recoverable from GR. Snapping dips to the round grid merely discretizes the error (10.35 → 10.4+). Even knowing the labels are human-drawn does not rescue us, because the hard quantity — where the geologist put a kink — is set by the unobservable geology.
We built a full research harness (773-well feature cache, whole-well holdout, augmentation, EMA, a GPU training stand) and swept a broad architecture space. Every from-scratch model floors near ~11 = the isolated-PF level.
Figure 5 (real holdout RMSE). Twenty-two architectures, coloured by family. The reference lines mark flat (15.1), our best NN (WARP, 11.3), our PF submission (7.09), and the leaders (5.26). Two clusters are worth naming: the continuity-anchored nets (orange, WARP family) that reach ~11, and the GR-trusting aligners (dark red, 2D-SDF / soft-argmax / surface-space) that blow up to ~30.
| Architecture | Holdout RMSE | Failure mode |
|---|---|---|
| flat baseline | 15.1 | — |
| Point-wise TCN (regress TVT) | 15.0 | no per-point signal → ≈flat |
| Neural matcher (static anchor) | 14.95 | collapses to flat |
| Neural matcher (iterated) | 101 | diverges (positive feedback) |
| GRU sequential filter | 14.7 | tiny safe steps ≈ flat |
| Contrastive GR↔typewell matcher | 179 ft loc. | GR self-similarity (§6) |
| Neural grid Bayesian filter (PF) | 24.5 | learned GR emission net-harmful |
| WARP (dTVT integration + cross-attn) | 11.28 | ★ best; continuity-anchored |
| WARP + multi-scale GR | 11.19 | marginal |
| WARP + multi-scale + EMA | 11.34 | stable |
| Surface-space (−Z) regression | 30 | drift; ill-conditioned |
| Low-DOF / spline head | 12 | — |
| Alignment (soft-argmax over typewell) | 30 | GR wall |
| Hybrid (WARP + low-passed align anchor) | 11.5 | align adds nothing |
| Mixture-Density Network (K=3) + Viterbi | 14 | fixes mean-collapse but weak |
| Synthetic pretrain (naive) | 13.2 | too-clean GR → no transfer |
| Joint real + synthetic augmentation | 11.57 | ≈WARP, less overfit |
| 2D misfit-heatmap + SDF U-Net (per-column) | ~29 | GR wall (Fig. 11) |
| 2D-SDF + Viterbi continuity decode | ~32 | continuity can't pick the true contour |
| Transformer (global self + cross attention) | 13.4 | overfits 773 wells |
| Learned stack / distillation of PF signals | 10.7 | = isolated-PF (signals correlated) |
| Pure classification over typewell bins (softmax, argmax decode) | 29.8 | no continuity anchor → GR wall |
| Pure classification, top-3-expectation decode | 28.6 | softens bimodal collapse, still hits the wall |
Why WARP (11) is best. It predicts a per-step derivative dTVT, integrates it by cumulative sum
anchored at the last known TVT, and treats GR only as a weak corrector via cross-attention to the typewell.
This is the weak-GR/strong-continuity principle of §6 made into an architecture: the output is
well-conditioned (it cannot drift far from the anchor) precisely because it never trusts GR to lead.
Why the neural matcher diverges to 101. When we let the matcher iterate — re-anchoring on its own GR match each step — it forms a positive-feedback loop onto a self-similar look-alike and runs away. The static version simply collapses to flat instead. Both are the wall in different clothes.
Why the learned PF (neuro-grid Bayesian filter) is worse than the classical PF (24.5 vs 11). Making the GR emission likelihood learnable let the network increase its reliance on GR, which is exactly wrong: the classical PF's hand-set, deliberately-weak emission is better than any likelihood the net learns, because the informative move is to distrust GR.
Why transformers do worse (13.4). With only 773 wells, global attention overfits; the CNN's locality is the correct inductive bias. Flexibility is a liability when the data are few and the signal is a fragile low-frequency trend.
Why 2D-SDF (the geosteering-image approach) caps at ~30. The misfit image (Fig. 11) has many plausible continuous zero-contours; neither a 2D receptive field nor a Viterbi decode can pick the true one, because there is no disambiguating signal. Continuity smooths the wrong contour just as happily as the right one.
Why pure classification over typewell bins fails (28.6–29.8), and why this is an independent confirmation. A separate research thread proposed a literal reading of "the geosteering-image approach": discretize the typewell axis into bins and predict each step's position via softmax + cross-entropy, decoding by argmax (or a top-3-probability-weighted expectation, to handle bimodality without the mean-collapse of a soft-argmax). We built and trained this from scratch, on the same encoder/cross-attention scaffold as WARP, for a clean architecture-only comparison. It reaches only 28.6 (top-3) / 29.8 (argmax) — squarely in the alignment/2D-SDF cluster (~29–32), not near WARP's 11. Top-3-expectation decoding softens the naive mean-collapse a little but does not touch the underlying problem: without a continuity anchor, the model has no reason to prefer the true bin over any of the other equally-plausible ones in Figure 11's misfit ridges. This is the fourth independent architecture family (after alignment, 2D-SDF, and the neural grid filter) to hit the same wall for the same reason, which is why we treat "weak-GR/strong-continuity beats explicit matching" as a structural property of this task rather than an artifact of one architecture.
Why naive synthetic pretraining fails (13.2). A generator with clean GR = typewell_GR(TVT) is
trivially invertible, so the pretrained model learns a direct inversion that collapses to flat on real,
self-similar GR. The joint real+synthetic variant regularizes a little (11.57) but does not transfer new
skill. Realistic synthetic — matching the real ambiguity — is required. The obvious next question is
which kind of realism matters, which we isolate in the controlled study below.
Because realistic synthetic pretraining is widely believed to be the decisive ingredient for the leaders'
scores, we ran a controlled experiment to find what about the synthetic is the bottleneck. We first
verified the premise of the whole "inverse-problem" family with a forward-model diagnostic on 160 wells:
the calibrated horizontal GR at the true TVT correlates 0.70 with the typewell prediction, the forward
model is locally discriminative (a ±15–40 ft shift raises the misfit by 3.8× on 98% of wells), and — key
for the diffusion hypothesis — the residual observed − typewell(TVT) is structured, with an
autocorrelation length of ~50 samples (i.e. not white noise; a naive Gaussian is the wrong noise model).
We then built a synthetic generator whose TVT paths use our own human-markup findings (§8.7): piecewise- linear, near-quantized dips, with rare fault jumps. Onto the clean forward-model GR we added noise two ways: (a) naive white Gaussian, and (b) the empirically bootstrapped real residual — i.e. the true, autocorrelated geological noise resampled from real wells. Bootstrapping the real residual is the best-possible noise realism, an upper bound on what any diffusion noise model could achieve. We evaluated transfer to the real holdout under two protocols: synthetic-only, and the leaders' recipe of synthetic-pretrain → real-finetune, against a real-only WARP anchor.
Figure 14 (real holdout RMSE). The result is unambiguous and, at first, counter-intuitive:
| Condition | Real holdout RMSE |
|---|---|
| real-only WARP (anchor) | 11.03 |
| synth-pretrain → real-finetune (the recipe) | 11.47 |
| synthetic-only, naive Gaussian noise | 14.86 (≈ flat) |
| synthetic-only, realistic bootstrap noise | 16.69 |
Two things stand out. First, the more realistic noise transferred worse (16.69 vs 14.86): the naive model safely collapsed toward flat, whereas the realistic-noise model confidently learned synthetic-specific moves that are wrong on real wells. Second, and decisively, pretraining then finetuning slightly hurt the real-only anchor (11.47 vs 11.03). Feeding the model the exact empirical noise distribution — better than any diffusion could reproduce — did not help. We therefore conclude that the synthetic bottleneck is not the noise model but the forward model: a single typewell plus synthetic trajectories does not reproduce the real joint GR↔TVT structure (lateral geological variation, typewell non-representativeness). Closing that gap requires a genuine physical formation simulator (multi-typewell, faulted, laterally heterogeneous), not a better noise generator — a substantially larger and less-defined undertaking than the "learn the noise with a diffusion model" recipe suggests. This is, to our knowledge, a novel and useful narrowing of why synthetic pretraining is hard on this task.
WARP alone (11.0) is far weaker than the classical pipeline (~7.1), so we asked whether it is at least
differently wrong — i.e. whether its errors are decorrelated enough from the pipeline's to be worth
blending, the same logic that produced our one confirmed transferable gain (§7). We ran WARP inference
on the same 160 held-out wells used by our full-pipeline proxy (§7) and measured the error correlation
between WARP and the tuned sp45/GBM pipeline output: only 0.52 — meaningfully decorrelated,
consistent with WARP's design (it deliberately does not trust GR the way the classical stack's GR
emission and alignment stages do). Blending (1 − a)·sp45 + a·WARP was evaluated with a proper
cross-fit (optimal weight fit on one half of the 160 wells, applied to the untouched other half, and
vice versa): the blend improved pooled RMSE in both directions of the split (proxy: sp45-only
10.62 → blended ≈ 9.8–10.2 depending on weight; never worse in either half). This is a materially larger
offline effect than the wall-hedge finding below.
We also tested combining this blend with a simpler "shrink toward last known TVT" hedge on low-confidence wells, and found the hedge became redundant once WARP is blended in — the jointly-optimal hedge weight collapsed to zero on both cross-fit directions, because WARP's own continuity anchor already supplies that effect. The two should not be stacked.
Caveat, stated plainly: this result is measured on our full-pipeline proxy, not the actual 7.08 submission pipeline, so the magnitude of any real leaderboard gain is unknown — the proxy is a weaker approximation of the real pipeline, and prior experience on this task (§13, lesson 1) is that isolated/proxy wins do not always transfer. We built a submission that blends a WARP checkpoint into the real pipeline at a conservative weight (0.15, versus the proxy-optimal 0.25–0.30). This submission has since been made and scored 6.882 (before the placement fix) / 6.846 (after) — a real gain over the 7.080 baseline (§7.2). We report the offline finding above as originally written because the methodology — measuring error correlation before blending, and cross-fit-validating the weight rather than reading it off a single split — is itself a reusable contribution, independent of the fact that it happened to also transfer here.
A real-LB test of pipeline placement, and a correction to our first read of it. We first placed this
WARP blend (and the physics post-process and pf_z blend of §7.1) after the pipeline's final blend but
before its train-contact override and its gold visible-prefix calibration stage — the same position we
had used for the simple wall-hedge (shrink toward last-known TVT on low-confidence wells, described just
above). We then submitted the wall-hedge variant on its own and it scored worse than the unmodified
pipeline on the real leaderboard (7.252), despite the hedge being honestly cross-fit validated as a real
gain on our proxy (§7, five independent splits agreed). Our first hypothesis was pipeline placement: the
gold-calibration stage runs last and makes its own per-well decision — by its own design comment, it
backtests a candidate correction on the visible prefix and only overrides the current submission when that
backtest says the candidate wins, treating "the current submission" as its anchor — so modifying that
anchor before gold runs, with a lever gold was never calibrated against, could plausibly confuse those
per-well decisions. We moved all three of our new stages — WARP blend, physics post-process, and pf_z
blend — to run after gold-calibration completes, and resubmitted every variant in both placements to
test this directly (§7.2).
The placement-crossed real-LB test (§7.2) only partly bears this out. WARP-blend and WARP+physics-pp did improve slightly under the after-gold placement (6.882→6.846, 6.881→6.836) — consistent with the placement mechanism above, and this is where our best submission (later refined to 6.794, §7.2) comes from. But wall-hedge, tested in both placements, is not rescued by the fix — it scores 7.252 before and 7.304 after, i.e. no positive effect from reordering, if anything the reverse. We therefore retract the strong form of the claim above ("this can flip a cross-fit-validated gain into a real regression"): placement is a real, small, second-order lever for components that are already net-positive, but it was never the dominant cause of the wall-hedge failure. The plainer explanation is that the wall-hedge mechanism itself — an unconditional shrink toward the last known TVT — is harmful on the real hidden test regardless of where it runs, a genuine proxy-to-real transfer failure independent of pipeline ordering. See §7.2 for the full placement-crossed table and the parallel finding for the 3-lever stack.
We separately tested a more sophisticated alternative to the simple wall-hedge: a LightGBM meta-model trained (via grouped cross-validation, no leakage) to predict the pipeline's absolute error from 16 GR-misfit and geometric features, then using its out-of-fold prediction to gate a per-point shrink toward last-known TVT. This underperformed the plain constant-weight hedge (11.12 vs 11.10 on the same honest split) — its correlation with the true error was only 0.24, weaker than the PF seed-spread signal (+0.48, §11) already in hand. We record this as a clean negative result: added model complexity did not buy a better uncertainty signal than the one we already had.
Figure 9 (real public LB, 4,065 teams). The full public leaderboard. The flat baseline (15.9) sits near the bulk's right shoulder; the median team scores ~9.9; only 7 teams beat 6.0, and the best is 5.26. Our best submission, 6.794 (§7.2, up from an earlier 7.09), sits at the edge of that top group. The shape of this distribution is itself evidence of the wall: the mass of the field is compressed into a narrow band a little better than flat, and the leaders' separation is small in absolute feet — consistent with a task whose irreducible floor is only ~1.5 ft below the best public score.
Three usable uncertainty signals emerged. (a) The PF seed-spread correlates +0.48 with the actual error magnitude (Fig. 7) — we can predict where the model is uncertain (though not which way to correct, §6). (b) The MDN head yields a full posterior per point (mixture means/variances/weights); its variance flags the bimodal (±15 ft Eagle Ford) mode-ambiguity zones. Crucially, the bimodal tie-break is a coin flip (mode correct 48.8%, r=0.054), so the honest uncertainty statement is that a large share of the error is aleatoric — irreducible from the observations — which is itself a calibrated, useful conclusion. (c) We trained a LightGBM classifier (5-fold CV) to detect, from leak-free per-well uncertainty features (PF seed-spread aggregates, PF/beam disagreement, eval-zone length), whether a well will land in the worst quintile by pooled error. It reaches AUC 0.65 — real, ordered failure detection, on par with a similar detection-vs-actuation measurement independently reported for this competition (AUC 0.69) — while, exactly as in that measurement, the sign of the error stays unpredictable (§6, angle 5). This is the same detection/actuation split stated more sharply: we can rank wells by expected pain; we cannot tell which way they will fail.
Our best components are physically grounded: the decomposition TVT = surface − Z is the geosteering datum
relation; the winning ensemble is variance reduction over a Bayesian sequential filter; the WARP model reads
the typewell as a "ruler" via cross-attention — the computational analogue of a geologist correlating logs.
The central negative result is itself physical: the eval-zone dip changes at sub-seismic faults whose
locations are not encoded in the observable GR, so the residual error is a property of the geology and the
measurement, not of modeling effort.
The identifiability argument in §5 (dip error as a constant of integration, growing unbounded over the eval-zone lever arm) is not a coincidence specific to this dataset — it is a structural fact familiar from navigation and inertial-observability theory: a constant bias state is unobservable from rate/increment measurements alone (a classic dead-reckoning result), and only becomes observable given an external absolute reference. Here, the GR log gives increments of rock character, not an absolute depth reference, so the per-well datum offset plays exactly the role of an unobservable bias state — consistent with why every matching approach we tried (§6, §8.2) can reduce local ambiguity but not resolve the global offset, and why the only well-conditioned strategy is to never let that unobservable quantity accumulate error unchecked (i.e., stay locally anchored, §5).
- Isolated-component tests lie. Denoise (+2.8% isolated → −0.24 LB) and the GBM blend (−6% isolated → +5% worse LB) and a 4-way ensemble (best holdout → worst LB) all looked good in isolation and lost on the real objective. Only full-pipeline / whole-well-holdout evidence transferred.
- Public LB ≈ seed noise for the PF cluster; treat any change < ~0.07 as noise, and prefer variance-reduced (more-seed) submissions for private-split robustness.
- Know where the error is vs which way to fix it. Seed-spread predicts error magnitude (+0.48); nothing predicts its sign. That distinction is the whole game.
- Variance reduction beat cleverness. Our two robust real-LB gains both came from decorrelating the estimator (a diverse PF partner, then a decorrelated neural corrector) — not from new physics, features, or architectures.
- On a time-boxed code competition, the runtime budget is part of the model. Parallelizing candidate generation (joblib) bought back the compute that a decorrelated ensemble and more seeds consume, which is what let our variance-reduction gain fit inside the 9-hour limit — an engineering lever as decisive as any modeling choice.
- On small geosteering datasets, weak-GR + strong-continuity beats explicit alignment, and simple inductive biases (CNN + anchor) beat flexible ones (transformer).
- Corrections do not compose indefinitely, even when each is honestly validated. Two independently
cross-fit-validated, real-LB-confirmed corrections (a decorrelated neural net, a physics post-process)
stacked cleanly (7.080 → 6.836); a third, equally well-validated correction (
pf_z) broke the combination outright (→ 7.446–7.515), in a controlled test crossed against pipeline placement (§7.2) that ruled out ordering as the explanation. Validate the whole stack you intend to ship, not just its latest addition.
Every number is from the whole-well holdout or the real public LB, never per-well averaging. Every figure in
this note is generated from the competition data, our 773-well method cache, or the public leaderboard CSV
by a single script (make_figs.py), and the caption states its source. The pipeline notebooks, the full
experiment log (TESTS_LOG.md), the NN research harness and roadmap (NN_RESEARCH_PLAN.md,
NN_PLAN_V2.md), the final NN analysis (NN_FINAL_ANALYSIS.md), and per-run results (RESULTS.jsonl) are
included. We build on the public PF pipeline and the diagnostic framing of the two traps (CV→LB mirage +
seed/refork variance) and the field-grouped "wall test" due to Georgy Mamarin, independently reproduced by
another competitor (wharekawa); our findings converge with theirs.
Limitations. (i) Our best submission builds on a public pipeline; our own contribution is the
variance-reduction ensemble and the analysis, not a new end-to-end model. (ii) The neural study, though
broad, was compute-bounded (a single modest GPU) — larger models / longer schedules might shift absolute
numbers, though the relative ceiling (~isolated-PF) was consistent across scales and architectures. (iii)
We did not achieve a working synthetic-pretraining pipeline; §9.1 shows why — the bottleneck is the
forward model, not the noise generator. (iv) A claim we made, had to retract, and have since traced to
the mechanism level. The inherited public pipeline contains a train-contact override that resolves a well
near-exactly (~0.01 RMSE) when its identifier also appears in the training set. Reasoning from the gate's
code alone (if wid not in train_wells: continue) and our understanding that hidden test wells should have
no ID overlap with training wells except through the shared typewells, we initially concluded this
mechanism must be inert on the graded set. A real competition submission run then showed otherwise:
its own strict audit log reports guarded_contact_override as an active postprocessor, with the override's
own diagnostic text explicitly describing coverage gained "on hidden overlap wells."
We have since gone further and traced why it is so precise, rather than leaving it as an unexplained
number. The override's physical-sounding reconstruction is phys = ref_tvt − (Z − ref_col) (a geological-
marker-plus-trajectory estimate that never touches any true label), but it is then shifted by
offset = mean(TVT_true,train − phys), computed directly from the train copy's own true TVT column —
so the output is phys + offset = phys + mean(TVT_true,train − phys), which cancels almost the entire
reconstruction error whenever that error is close to a per-well constant. This is why it resolves to
~0.01 ft: not because the physical reconstruction is that precise on its own, but because the correction
term is calibrated directly against the true answer for what is functionally the same wellbore. We also
found this is not a single, toggleable code path: the same substitution is implemented redundantly in
three independent places in the inherited pipeline — a standalone postprocessor, a candidate inside the
gold-calibration stage's own backtest pool, and a third function named (in the original code)
_gold_reapply_guarded_contact_override, called unconditionally after gold-calibration for every blend
profile. Disabling any one of the three leaves the other two intact; we had to patch all three to get a
clean reading. We measured the magnitude directly on the three wells in our local development stub (which
are verbatim copies of specific train wells, used only for local testing): with all three layers active,
pooled RMSE on those wells is 0.0053 ft; with all three disabled, the same wells scored by our genuine
model stack (PF + beam + WARP-blend + physics post-process) give 6.47 ft — a three-orders-of-magnitude
gap that leaves no ambiguity about what the mechanism does when it fires.
What this does not change: because the override's behavior has been identical and unmodified underneath every submission we have made, it cannot explain the relative differences between our own variants (denoise, the decorrelated ensemble, more seeds, wall-hedge, WARP-blend, physics-pp) — those deltas are still honest, since the override runs constantly across all of them. What it does mean: our absolute LB numbers are not purely attributable to the components we deliberately engineered, and — unlike our first, narrower framing — this is not merely "a mechanism of unclear magnitude," it is a train/test answer substitution whose effect we have now quantified directly.
We went further and measured its real contribution on the actual hidden test, not just our local stub. We resubmitted our best pipeline (WARP-blend + physics-pp + the cross-validated weight, §7.2) with all three override layers disabled: it scored 7.155, against 6.794 with the override active — a real, measured contribution of 0.361 ft. Converting to squared-error terms (the metric the competition actually pools), this is ≈9.8% of pooled squared error on the graded rows, under the simplifying assumption that override-affected rows carry roughly the pipeline's typical honest error before correction. This is a small but real minority of our overall gain (flat baseline 15.9 → honest 7.155 → 6.794 with the override): most of what separates us from flat is genuine engineering, but a real, now-quantified fraction is not. It also directly contradicts the inherited pipeline's own diagnostic comment, which asserts "current public test = train-contact wells only; override determines them" — if the entire public test set carried this ID overlap, disabling the override would collapse performance back toward the isolated-pipeline level (8–10+ ft), not move it by 0.36 ft. The real fraction of the hidden test set with this overlap is evidently modest, not total, contrary to what the inherited code itself assumed. We flag all of this as prominently as we know how, rather than quietly softening the earlier text, because catching our own overclaim with real evidence — three times now — is exactly the standard we are holding the rest of this note to.
Future work (the path to the leaders' 5.2–5.4). Synthetic pretraining remains the most likely route, but §9.1 sharpens the target: a better noise model (e.g. a 1D diffusion / neural-SDE fit to the residual) is not the missing piece — we showed that even the exact empirical noise fails to transfer. What is needed is a better forward model: a physical formation simulator with multiple typewells, explicit faults, and lateral heterogeneity, so that synthetic GR reproduces the real joint GR↔TVT ambiguity rather than a clean, single-typewell inversion. Only then should one layer on realistic noise, bimodal ±15 ft jumps, and miscalibration, and fine-tune on the 773 real wells behind a transfer gate (a synth-trained model must reach ~11 on the real holdout, not ~0 on a synthetic one). Complementary directions: distilling the full 7-pipeline (not the isolated PF) into a compact model; and combining the MDN head with a 2D misfit-SDF backbone once realistic priors are in place. Our analysis suggests these are necessary because the raw GR signal is broadband-unreliable — the gains must come from a better prior, learned from a genuine synthetic geology, rather than from the observation likelihood or the noise distribution.
A new architecture line, and a near-miss worth documenting. We built a duration-aware beam-search
decoder (a Hidden-Semi-Markov model over piecewise-linear segments, with a mixture-hazard segment-length
prior and AR(1) dip-persistence, both fit from our own known-zone data) as a genuinely different motion
model from the PF's continuous AR(1) diffusion — inspired by the category of the joint (segment-length,
Δposition) decoding idea, not any competitor's numbers. After fixing two real bugs (fitting priors on the
wrong tracked quantity, and a catastrophic-divergence failure mode on structurally "wiggly" wells, cured by
a two-component hazard plus diversity-preserving beam pruning), it reaches rough parity with our isolated
pf_ancc but shows no cross-fit-validated blend gain against the full production combo — confirmed
cleanly on a proper held-out well set, not just a small sample. Separately, while widening the WARP-blend
weight search past its previous grid edge (0.30), we found what looked like a dramatic further win (pooled
RMSE 8.58 → 7.06 at weight 0.85) — and then caught it: the WARP net was trained on 613 of the 773 wells in
that evaluation pool, so pushing weight toward pure WARP was leaning on memorized, not generalized,
predictions. Restricting the same test to WARP's true 160-well seed-42 holdout reversed the conclusion
entirely — 0.30 is the genuine optimum, exactly as shipped. We record this as a standing methodology rule:
any local evaluation touching a learned component must be restricted to that component's own true holdout,
never a pool it was partly trained on.
The ROGII task decomposes cleanly: the high-frequency TVT wiggle is free (it equals −Z, which is known at eval time), and the entire difficulty is a smooth per-well surface trend whose slope-changes occur at sub-seismic faults that the self-similar GR log cannot localize (broadband-irreducible error). This is why the trivial flat baseline is so strong, why a weak-GR/strong-continuity prior wins, and why 60+ experiments and 22 neural architectures — MDN, synthetic pretraining, 2D misfit-SDF, transformers — all cap at the isolated-PF level (~11) while the tuned classical pipeline reaches ~7 through its full stack. Our first concrete, transferable gain came not from new modeling but from variance reduction (a decorrelated PF ensemble, 7.230 → 7.091). A second, larger real-LB gain then came from stacking a decorrelated neural corrector with a robust physics post-process, 7.080 → 6.836, further refined to 6.794 — our best submission — by transferring a cross-validated hyperparameter back onto the real pipeline, paired with a controlled real-LB negative result showing this stack does not extend to a third, individually-validated correction (§7.2), and a correction to our own earlier causal claim about why the first such attempt (wall-hedge) failed. We hope the map of where the signal is and is not is useful: on this task, measure twice on a whole-well holdout, distrust the public LB, separate the recoverable (the −Z wiggle) from the physically unrecoverable (the cross-field surface trend) — and even once a gain is real-LB-confirmed, test whether it still holds before stacking one more thing on top of it.
Acknowledgements: public PF pipeline and the two-traps / wall-test diagnostic framing by Georgy Mamarin; independent reproduction by wharekawa; leaderboard context from Rishikesh Jani and Tucker Arrants.
For quick reference, the full list of experiments referenced above, by section:
- §8.1 Baselines (3): flat; linear extrapolation; pooled-RMSE methodology fix.
- §8.2 GR matching (9): Pearson window; banded tracker; fixed-anchor; heel affine calib; NCC-in-PF; shape/derivative; affine-in-beam; full bidirectional DP; trajectory-informed DP.
- §8.3 Particle filter (10): affine-in-likelihood; resample threshold; adaptive scale ×2; lo-noise ensemble ✅; gs-decorrelation; Student-t noise; typewell-jitter; 4-way kitchen-sink; runtime-guard split.
- §8.4 Post-processing (5): Savgol/poly; deg-2/deg-4; piecewise-linear; physical clipping; bimodal hedge.
- §8.5 GBM/ML (8): GBM standalone; PF+GBM isolated ✅; PF+GBM on LB ❌; meta-stacker; Q-3D tortuosity; signed azimuth; confidence blend; blend-weight sweep.
- §8.6 Denoise/external (3): rotation-band denoise; toolkit mining; lineage analysis.
- §8.7 Human markup (3): dip-snapping; PL reconstruction; formation-intersection kinks.
- §7.2 Real-LB stacking/placement confirmation (2): placement-crossed WARP+physics-pp resubmission ✅ (new best 6.836); placement-crossed wall-hedge and 3-lever full-stack resubmission ❌ (both harmful regardless of placement).
- §7.2/§7.3 Overfitting and validation-honesty checks (5): 5-fold grouped CV of the new best (5/5 folds positive, identical hyperparameters every fold) ✅; real-LB transfer of the CV-selected WARP-weight (0.15→0.30), a further gain to our current best 6.794 ✅; hedge-on-bare-base vs hedge-on-tuned-combo cross-fit, confirming the hedge collapses to weight 0 once WARP+physics-pp are applied ✅; LSO spatial K-means-block holdout, confirming the gain is not neighbour leakage ✅; isolation-quartile check, confirming isolated wells benefit more, not less, from the new combo ✅.
- §15 Real-LB audit of the inherited override (1): resubmission with all 3 override layers disabled, measuring its real contribution directly on the hidden test (7.155 honest vs. 6.794 with it active, ≈9.8% of pooled squared error) ✅.
- §9 Neural nets (20): see the architecture table.
Total: 60+ distinct experiments.