What makes a layer droppable? An exact-mask MNIST test of the Fable hypotheses

Completed exploratory checkpoint audit, 9 September 2026. We evaluated every combination of four removable branches in 30 existing checkpoint states, then fitted and froze inexpensive image-based routing policies before opening their test outcomes. No neural networks were retrained for this audit.

The evidence supports a specific claim: stochastic-depth training can create functional redundancy in these tapered residual MLPs. At the primary, validation-selected checkpoint, decreasing SD reduced deletion-induced cross-entropy by 0.0588 nats relative to residual-dense training, with a three-seed paired 95% interval of [−0.1036, −0.0140]. The higher-order fraction of centered-logit mask interactions fell from 13.31% to 2.33%. Neither result establishes better full-model accuracy.

The broader story is less favorable. The apparent advantage of digit 1 over digits 4 and 9 became uncertain after margin adjustment. Direct gradient predictions ranked deletion damage well at selected checkpoints, but their ranking deteriorated at the final checkpoint and the finite-difference directional probes had substantial numerical error. A shallow input router saved nominal MACs, yet exceeded its test error tolerance in five of nine primary cases and ran slower than dense inference. These distinctions matter when translating an appealing geometric explanation into an actual inference policy.

Reading the controls

The layer-scope selector now offers all six learned layers or the original four middle branches. In the original scope, unchecking everything still leaves the learned feature layer (stem) and classifier (head). The stem maps 784 pixels to 2,500 ReLU features; crops retain the first 500, and the classifier produces ten digit scores. This trained shallow predictor uses 16.42% of the counted affine work. In the extended scope, dropping the stem inserts an untrained zero-padded pixel representation. Dropping the classifier means no prediction: coverage and correct outputs fall to zero, while classification accuracy is undefined. Uniform random guessing would average 10%, not zero.

SD means stochastic depth: randomly skipping whole branches during training. “Constant SD” uses fixed drop probabilities of 10%, 20%, 30%, 40%, from the first to last branch. “Decreasing SD” starts at 20%, 40%, 60%, 80% and reduces them linearly to zero by epoch 100. Its average number of active middle branches therefore increases from two to four. Both recipes drop later branches more often; “decreasing” refers to drop probability over training, not to the number of active layers. No recipe that increases dropout over time was tested here.

The method selector chooses already-trained weights. Fixed inference uses the checked layers for every image. Random inference makes checked layers eligible for independent dropout at the slider's probability; unchecked layers always remain. Its scores are exact expectations over single mask draws, not a prediction ensemble. Retained branches use gain one (no rescaling), and neither mode retrains the model. A validation-selected checkpoint can occur before the decreasing training schedule reaches zero.

Six-layer inference follow-up: the learned input representation matters

The extended explorer adds two switches: the learned feature layer and the classifier. It enumerates 64 settings on the same 30 frozen checkpoint states, using all 10,000 official test images. No network was trained or checkpoint selected again. Every original four-branch mask is reproduced exactly. This remains exploratory analysis of an already reused test set.

Six mask bits read stem → branch 1 → branch 2 → branch 3 → branch 4 → classifier. 111111 keeps everything; 100001 keeps only learned features and the classifier; 000001 keeps only the classifier; 000000 abstains. These are displayed bit strings, not conventional most-significant-bit-first binary notation.

Dropping a layer must specify what replaces it. Removing the stem inserts normalized pixels followed by zeros to reach 2,500 coordinates. Removing a middle branch retains the first coordinates needed by the next layer, followed by ReLU. Removing the classifier emits no digit and exits before any affine computation. Only middle branches were eligible for stochastic depth during training: endpoint deletion tests an untrained intervention.

Measured classification outcomes

Each entry below is a mean over three training seeds. All four columns retain the classifier, emit a prediction for every image, and therefore have 100% coverage. “Stem removed” retains all four body branches. “Classifier only” passes padded/cropped pixels directly to the saved classifier; it is not a newly trained linear MNIST model.

Tolerance to missing middle computation does not imply tolerance to missing learned input features. In the selected SD checkpoints, dropping all four middle branches retains 95–96% accuracy, while removing the stem alone leaves about 12%. The zero-padded replacement changes the representation drastically. This establishes dependence on the learned stem under this replacement, not a theorem that every possible alternative stem must fail.

“Classifier only” spans 9.48–20.97% across the 30 individual checkpoint states. It still processes image-dependent coordinates with learned classifier weights and biases; it is not uniform random guessing. Removing more layers need not lower accuracy monotonically: for some checkpoints, the classifier-only intervention is more accurate than keeping all four branches after removing the stem. Neither intervention preserves useful MNIST quality.

What zero means when all layers are dropped

With no classifier there are no ten class scores to compare. The policy abstains. We report three distinct quantities:

All 32 settings with the classifier absent implement this same abstention policy. They add no classification measurements and should not be read as 32 independent failures. Cross-entropy is also undefined. A hypothetical network forced to guess a digit after removing all computation would instead have a guess-dependent accuracy; uniform random guessing averages 10%. Forcing the displayed classification accuracy to zero would misdescribe that experiment.

Random dropout during inference

Choose the layers eligible for dropout and set a shared probability p. Each eligible layer is dropped independently for each input. Ineligible layers stay present. A mask with d dropped and k kept eligible layers has probability p^d (1−p)^k; masks dropping an ineligible layer have probability zero. The page sums the measured outcomes of all masks with these weights. Its plots are exact expected single-draw scores, not a Monte Carlo estimate and not an ensemble formed by averaging logits or probabilities. “Draw one random mask” shows one example outcome; changing that draw does not change the aggregate scores.

If the classifier is eligible, coverage is exactly 1−p. Correct-output rate is coverage times accuracy conditional on a prediction. At p=1, coverage and correct outputs are zero and conditional accuracy is undefined. If only the four middle branches are eligible, coverage remains 100% even at p=1: the trained shallow predictor remains. Checking no eligible layers makes the policy identical to full inference at every slider position.

Surviving branches use gain one. We did not evaluate inverse-survival rescaling at inference. The computed curve is therefore a deletion policy on saved weights, not a replay of the scaled stochastic-depth training network. Expected MAC counts are arithmetic counts only: this follow-up did not measure the overhead or latency of a per-image random-mask implementation.

Verification and reproducibility

The three successful A100 jobs evaluate 32 classifier-present masks per checkpoint. Every full-mask forward matches the saved model's ordinary forward bitwise. The 16 embedded original masks reproduce all 4.8 million archived test predictions exactly; labels, dense error indices, checkpoint hashes and dataset hashes also agree. Mean cross-entropy agreement uses the original absolute tolerance of 0.00003. The 1,408 previously selected gallery entries remain unchanged; no new examples were selected based on this follow-up.

The extended JSON contains 1,920 mask records, including the explicit abstention settings, plus per-digit metrics and frozen-gallery predictions. NPZ sidecars preserve all per-image predictions and losses; abstention uses prediction −1 and undefined loss. These masks and images do not increase the number of independent training seeds.

The three successful jobs ran in parallel on A100-SXM4-40GB GPUs and took approximately 22–34 seconds each inside the evaluator. An earlier wrapper-import failure was fixed before the evaluator ran, and both attempts' reservations and records are retained. The closing provider meter increased by $0.08524 for this follow-up, to $5.08899 in the shared MNIST environment. Both apps were stopped with zero tasks. The conservative shared reservation bound, including the failed attempt, is $10.42982, below the original $30 cap and the $24 stop guard. Metering is a provider snapshot, not a final invoice. Closing cost and shutdown receipt.

Six-layer protocol · Evaluator · Frozen specifications and raw results · Extended explorer data

What was tested

The frozen protocol specifies five tests: deletion resilience, class differences after margin adjustment, directional sensitivity, mask interactions, and adaptive routing. The starting checkpoints come from the controlled stochastic-depth study, with seeds 101–103. Residual dense, constant SD, and decreasing SD supply the central 18 checkpoint states: three recipes × three seeds × two endpoints. Residual plus unit dropout supplies six secondary states; six plain-MLP states supply a deliberately disruptive surgery diagnostic.

The primary endpoint is the checkpoint selected by validation cross-entropy. Epoch 100 is a separately reported secondary endpoint. These are repeated measurements of the same training runs, not six independent seeds. Each interval below uses three seed-level estimates or same-seed differences, Student's t with two degrees of freedom. Masks and test images are not counted as independent model replications. The intervals are descriptive, unadjusted for the many reported comparisons, and can be wide; an interval including zero does not establish equivalence.

The network has widths 784→2500→2000→1500→1000→500→10 and 11,972,510 parameters. Its four eligible middle transitions have a prefix-crop shortcut followed by ReLU. The learned stem and classifier remain compulsory in this original four-branch audit; the separately reported six-layer follow-up removes that restriction. Cropping loses coordinates and widths change, so this architecture is not an invertible, equal-dimensional flow. The main models use normalized inputs and linear output logits; original raw-input/ReLU-output fidelity runs are outside this audit.

A four-bit integer identifies the retained branches, shallowest first: mask 15 keeps all four and mask 0 removes all four. Retained branches have gain one at inference. SD training used inverse-survival gains, so an unscaled deletion network is not exactly the corresponding conditional training network. The primary deletion panel is the six masks retaining exactly two branches: 3, 5, 6, 9, 10, and 12, equally weighted. Half the eligible branches does not mean half the network or half the work.

Nominal affine MACs are 1,965,000 + 5,000,000*b0 + 3,000,000*b1 + 1,500,000*b2 + 500,000*b3, versus 11,965,000 for the full model. The primary panel averages 58.21% of full affine MACs. Biases, ReLU, memory traffic, routing, and indexing are outside that count.

The official MNIST test set and these seeds were already used in earlier experiments, including test-targeted baseline optimization. The original validation set also selected learning rates and checkpoints. The new policy split and frozen choices protect this particular routing comparison from direct test fitting; they cannot make the overall investigation an untouched confirmatory evaluation.

H1: stochastic depth reduces deletion damage, but quality must be measured separately

For each mask, excess CE is its loss minus the same checkpoint's full-model loss. Negative values are retained. Harmful flips are full-correct predictions made incorrect by deletion, with all image/mask pairs as the denominator; repaired full-model mistakes are recorded separately. The following are three-seed means over the six two-branch masks. Accuracy columns are percentages; CE is nats per image.

The primary paired comparisons use SD minus residual dense. A smaller excess CE means less deletion damage, while absolute masked accuracy answers a different question.

Decreasing SD supports the primary directional redundancy hypothesis on this panel. Constant SD has the same favorable direction, but its primary excess-CE interval includes zero. Neither selected-checkpoint SD comparison resolves an absolute masked-accuracy advantage: the starting full-model accuracy differs too. At the final checkpoint, both SD recipes retain markedly more accuracy after deletion. Their masked CE is also lower than their own full CE; this is a measured loss improvement, not by itself an identified calibration mechanism.

The secondary unit-dropout control does not reproduce the same resilience: at the selected checkpoint its accuracy falls from 98.330% to 97.443% and excess CE is +0.1928; at the final checkpoint, 98.507% to 97.788% and +0.0282. Ordinary unit dropout is not interchangeable with training the precise branch bypasses used at inference.

Plain-network surgery is catastrophic: selected accuracy falls from 97.913% to 8.621%, and final accuracy from 98.573% to 8.826%. Here a deleted affine/ReLU transition is replaced by a crop/ReLU that the plain model was never trained to use. This is evidence that the intervention is disruptive, not an architecture-only causal proof that plain networks cannot be compressed or re-encode information.

Removing every eligible branch is a useful secondary diagnostic

With all four body branches removed, accuracy is 93.507%, 95.370%, and 96.323% for selected residual, constant SD, and decreasing SD respectively. At epoch 100 the corresponding values are 93.163%, 97.310%, and 97.460%. Only 16.423% of nominal full MACs remain.

This is still a learned 2500-unit stem, successive prefix crops retaining 500 coordinates, and a learned classifier. It is not a zero-computation predictor or an early-exit head. These predeclared all-skipped measurements demonstrate substantial learned redundancy, but were not used to select a new deployment policy from test accuracy.

Branch importance is unequal. Removing the first eligible branch saves 5 million MACs: final residual accuracy falls from 98.400% to 97.640%, versus 98.443%→98.360% for constant SD and 98.510%→98.400% for decreasing SD. Later branches can cost much less accuracy. A uniform layer-count rule obscures both compute and functional differences.

H2: “digit 1 is easier to drop layers on” weakens after confidence adjustment

The predeclared contrast is resilience of digit 1 minus the mean resilience of digits 4 and 9, among full-correct examples. Resilience is the fraction of the six primary masks that remain correct. Positive values favor digit 1.

True-class-margin deciles were defined using full-correct policy-fit examples. Calibration data then froze common-support bins containing at least 20 full-correct examples of each target digit, and common bin weights. This standardizes each digit to a shared coarse margin distribution; it does not fully match individual examples or establish a causal digit effect.

All three primary adjusted intervals include zero. The raw ordering therefore does not support a reliable intrinsic class rule at this precision. Adjustment does not always reduce the estimate: selected residual increases in magnitude but becomes less precise. At the secondary final decreasing-SD endpoint, the raw positive contrast reverses to −0.119 pp [−0.185, −0.054] after adjustment. The final residual contrast remains positive; there is no universal disappearance of class association either.

The support and permutation results below show why a single attractive class ranking is insufficient. Coverage is the fraction of full-correct examples of digits 1, 4, and 9 retained in the frozen common bins. The JSON also reports a fraction using all ten digits' full-correct examples as denominator; that is a different quantity.

The table’s one-sided permutation p-values concern the digit-1-minus-mean(4,9) contrast. The separately recorded all-ten-digit permutation statistic is between-digit variance. The 1,000 within-bin permutations keep each example's six-mask result together and use frozen seed 20260913. Their p-values describe conditional label exchangeability within coarse margin bins; they are not three-seed replication tests, corrected multiple-comparison probabilities, or proof that digit identity causes resilience. Selected residual shows a positive adjusted association in all seeds, constant SD changes sign in seed 103, and decreasing SD has weaker per-seed permutation evidence. Between-seed variation remains important even when one per-example permutation p-value is small.

Every digit's counts, raw and standardized rates, and exploratory ten-digit rankings are available in the analysis artifact. Those additional rankings were not used to turn the primary digit-1 hypothesis into a favorable post hoc class rule. Confidence and labels here are analysis covariates, not free features available to an inference router.

H3: direction predicts damage at selected checkpoints; the final and numerical checks limit the claim

At a full block output h, deletion substitutes the same-width post-ReLU cropped bypass p. The actual intervention is delta = p − h, not simply the negative pre-ReLU branch output. On a fixed 128-example validation probe, the first-order prediction is the downstream CE gradient dotted with this delta. Norm and angle are alternative fixed proxies.

The table averages the four branch-wise Spearman correlations within a seed, then across three seeds. The SSE score is 1 − SSE(first-order prediction)/SSE(zero change), not the conventional R² relative to predicting mean damage.

At selected checkpoints, gradient predictions beat both proxies in all 36 central branch/seed cases. At final checkpoints their rank correlations collapse or become negative, despite high all-example SSE scores. A few large-damage, already misclassified examples can dominate squared error while many tiny changes have unreliable ranks. The selected full-correct-only mean block scores range about 0.47–0.89, substantially below the all-example scores. Thus the favorable selected result is not a universal layer-importance law.

The independent audit also identified a serious limitation in the Gaussian directional comparison. Changing finite-difference epsilon from 0.001 to 0.01 changes the estimated centered-logit response by 6–44% for selected deletion directions and 35–115% for selected Gaussian directions, measured as RMS disagreement relative to the epsilon-0.01 response; final Gaussian disagreement reaches about 120%. Even the last eligible branch, followed only by a linear classifier, has 6–44% deletion and 35–58% Gaussian disagreement at selected checkpoints. A numerical component is therefore demonstrated; ReLU boundary crossings cannot explain all of it. The relative contributions of cancellation and nonlinear crossings elsewhere are not isolated.

For final checkpoints, 102–119 of the 128 probe examples have dense CE below FP32 machine epsilon. An independently recorded post hoc threshold sensitivity improves some correlations, but does not replace the frozen all-example analysis. We regard the finite-difference Gaussian anisotropy comparison as numerically unresolved, and do not infer a global Jacobian bound, contraction, or a complete read/write circuit from it.

H4: stochastic depth reduces exact mask interactions, without making the network globally linear

All 16 masks permit exact Walsh and Möbius expansions on four binary gates. For the primary statistic, logits are first centered across classes, then each example's fraction of nonconstant Walsh energy at degree two or higher is computed. The reported mean averages those per-example fractions; it is not the ratio of pooled energies. No test example had an undefined near-zero denominator.

At selected checkpoints, constant SD minus residual is −11.003 percentage points [−12.135, −9.871], and decreasing SD minus residual is −10.979 [−11.492, −10.467]. Mean absolute higher-order energy also falls, from 0.6799 to 0.0533 and 0.0315 in centered-logit squared units. Thus the normalized effect is not just an expanding denominator. Full quality, total response scale, and architecture still differ between training recipes; this association alone does not identify why SD worked.

Exact binary-corner reconstruction is an algebraic check that every four-variable function passes, not evidence of actual linear interpolation. We also ran the network at withheld fractional gains 0.25, 0.5, and 0.75 for individual branches and along the all-branch diagonal. At selected checkpoints the mean centered-logit discrepancy from the full corner multilinear interpolant is 0.041, 0.037, and 0.058 RMS for residual, constant SD, and decreasing SD. The corresponding degree-one truncation errors are much larger: 3.656, 1.136, and 0.700. These interpolation errors are descriptive in logit units; a small normalized Walsh interaction fraction does not make every anchored degree-one approximation accurate.

Gate scaling is essential. The separately measured survival mixture compares the gain-one output with rho*F(1/rho) + (1−rho)*F(0) at each checkpoint's training survival probability. Inverse-survival scaling preserves the conditional mean of the gated affine contribution, not generally the downstream logits or expected loss. Nonzero mean-logit bias and CE Jensen gaps occur in the nontrivial probes. At the final decreasing-SD checkpoint, rho equals one: its zero mixture bias is an algebraic identity, not evidence for successful nonlinear averaging. Do not mix these scaled training probes with the gain-one inference deletion results.

CE has its own nonlinear interactions, even when logits are additive; its coefficients are not literal counts of computational paths. Low higher-order energy likewise does not bound the size of first-order deletion effects. The evidence supports a measured reduction in this mask-response statistic, not a claim that dropout works if and only if the rest of the network is linear.

H5: a calibrated tree saves nominal work, but does not establish a useful adaptive advantage

Each checkpoint received one multioutput CART tree: maximum depth three, minimum leaf size 200, fixed seed 20260909. Its 49 features are 7×7 averages of raw image pixels, requiring neither labels nor a full-model forward. Using the first 5,000 validation positions, it predicts each mask's error change relative to dense inference. Dense predicted extra error is fixed to zero.

The remaining 5,000 positions choose among a frozen grid of 11 accuracy/cost tradeoffs. Selection maximizes nominal MAC savings subject to at most ten net additional calibration errors, with deterministic tie rules and a full-model fallback. An independent static mask uses the same empirical tolerance. The random comparator shuffles the router's test mask assignments, preserving their exact realized MAC distribution while removing image-dependent assignment. This is one frozen shuffle, not an average over random policies.

The policy manifest was written and hashed before local test-outcome access. Audit jobs had already computed mask test arrays, but these were withheld from fitting and selection. The tolerance is an empirical 0.2-percentage-point rule, not a confidence-certified generalization bound. Repairs can offset harmful flips, so net error is not the fraction of originally correct examples harmed.

All nine primary quality/cost points follow. Static and routed policies can use different amounts of work; only the shuffled comparator exactly matches routed nominal cost. Test tolerance means no more than 20 net extra errors among the 10,000 test images.

Cross-entropy and separate harm/repair counts expose quality changes hidden by net accuracy. CE was recorded, but was not a post hoc policy-selection constraint.

Five of nine selected routers fail the test tolerance, despite meeting it on calibration. Only three of nine selected static masks meet it on test. Some reductions in nominal work are substantial, but the expected error constraint transfers imperfectly even within MNIST. There is no reason to rename the tolerance after observing failures.

Across seeds, the selected router-minus-shuffled accuracy differences are +0.023 pp [−0.015, +0.061] for residual, −0.023 [−0.160, +0.113] for constant SD, and −0.023 [−0.086, +0.039] for decreasing SD. The image-dependent assignments therefore do not establish an advantage over their own matched-cost shuffle. Router-minus-static accuracy intervals also all include zero, and those static comparisons are not matched in cost.

The final-checkpoint policies are secondary and do not rescue this claim:

The final decreasing-SD router saves the most nominal MACs on average but misses the test tolerance in all three seeds. More removable computation does not ensure that this particular coarse tree identifies the right examples or masks.

Actual A100 inference further changes the practical conclusion: the grouped router is slower than full inference despite its nominal MAC savings. The independently timed job includes image features, routing, gathering, affine calls, and scattering, and its predictions match the functional audit for all nine primary checkpoints. Static masks can run faster because they retain regular batches; their quality tolerance still often fails. The timing and cost ledger below distinguish these execution measurements from the affine-MAC estimates.

What this says about the Fable explanation and useful dropout choices

The accompanying mathematical audit supplies explicit counterexamples and qualifications. A residual update can re-encode coordinates: x + (A−I)x = Ax, including a rotation. Inverse-survival scaling does not make nonlinear outputs unbiased. A small angle is not the same as a small increment; a large radial rescaling can have zero angle. Deleting an ODE-like step does not automatically approximate a larger step over the original horizon. Small higher-order interaction energy does not bound a potentially large first-order loss effect. Those are mathematical limitations of the supplied argument, independent of whether these MNIST results are favorable.

The practical evidence favors testing dropout that matches an explicitly trained, dimensionally valid bypass and deployment convention. Whole-branch stochastic depth fits that intervention here; ordinary unit dropout supplies a weaker control for branch deletion. Preserve the distinction between training-time inverse-survival gains and gain-one inference masks. Start with a validation-selected, cost-aware static mask panel, report absolute quality alongside damage, and measure actual execution. Class identity or a full-model margin can diagnose confounding but is not a free routing feature. This particular shallow router adds overhead without a demonstrated assignment advantage; a different router or accelerator would require its own frozen quality and timing test.

The five hypothesis outcomes are therefore mixed: decreasing SD supports the primary redundancy contrast; a universal digit-class ordering does not survive the full adjustment and endpoint evidence; directional gradients are useful at selected checkpoints but numerically limited at final ones; SD reduces exact centered-logit interactions without proving global linearity; and this cheap adaptive router does not deliver a practical speed/quality win.

Verification, reproducibility, and limits

All 30 planned states and all 16 masks completed. The all-kept audit forward matched source logits bitwise on the 128-example direct probe, and original full validation accuracy/loss and full test accuracy/loss/error indices were verified. The older validation records contain no error-index lists. The independent audit checked 99 remote artifact hashes and sizes, 60 dense split references, and all 30 checkpoint states. Mechanistic probes used all 128 predeclared validation examples; none were reduced or selected for favorable correctness. Bulk-versus-probe predictions also agreed, while batch-shape logit differences were recorded. The compact per-example energy arrays reproduce the reported interaction fractions; the independent audit did not regenerate every transform from archived full logits.

The policy manifest SHA-256 is 6aff7b936f9ff89478536cbd9468727a1c63c7e3894da98ee5033e2999b0ad52. The recorded analyzer source hash matches the implementation used to fit it. The initial evaluation refusal concerned local wrapper JSON versus exact remote source JSON; retrieving the pinned originals resolved that provenance mismatch without changing scientific tolerances, policies, or fits.

Three seeds, one reused dataset, one tapered MLP architecture, reused validation selection, multiple exploratory comparisons, a 128-example mechanism probe, and unresolved finite-difference precision all limit extrapolation. The policies optimize calibration net error, not class fairness or confidence-certified risk. MACs are not energy or latency. Results at all-skipped masks, final checkpoints, unit-dropout controls, and plain surgery remain separately labeled secondary evidence.

The analysis JSON contains every planned checkpoint, all mask/class/example summaries, both endpoints, seed-level values and intervals, calibration candidates, policy outcomes, and artifact hashes. The independent check records numerical and provenance verification, including post hoc precision diagnostics. The policy manifest, analysis implementation, and audit implementation make the frozen choices inspectable. The routing summary records actual inference measurements.

Measured A100 latency: static masks win this implementation

The nine primary selected-checkpoint models were timed on one NVIDIA A100-SXM4-40GB, using PyTorch 2.14.0+cu130, CUDA 13.0, FP32 tensors with TF32-enabled high matmul precision. The full 10,000-image test set is already on the GPU. Batch size is 2,048; every method receives two warmup batches, then three synchronized whole-test passes in rotating order. The table uses the median of all three passes, in milliseconds per 10,000 images. It is throughput timing, not single-image or cold-start latency.

The input-dependent implementation includes average pooling, the decision tree, sorting, GPU-to-CPU mask counts, per-group gathers, genuine skipped affine calls and output scattering. The random comparator includes grouping but has preassigned masks. Checkpoint loading, initial host-to-device data transfer, fitting/calibration and verification are outside these inference timers. No compilation or graph-capture cost is hidden.

Across the nine per-model medians, dense inference takes 4.83 ms, static masks 3.45 ms, and image-dependent routing 13.59 ms. The router is 2.07–3.25× slower than dense inference on every model. Static masks are 1.19–1.93× faster, at the accuracy/cost points shown above. These masks were selected using validation; several exceed the empirical 0.2pp error tolerance on test, so speed is not an unconditional quality-preservation claim.

All nine CPU/GPU routing decisions and all 36 method/checkpoint prediction vectors match the exact-mask functional references. Observed numerical disagreement count is zero. Each raw timing pass is retained. These three repetitions on one assigned GPU do not constitute an independent hardware benchmark or a tuned lower bound on routing overhead. A fused or coarse-bucket router could behave differently; that remains untested.

Raw timing run · Compact timing summary · Timing implementation

Original four-branch audit: compute cost and execution

The fourth routing job took 17.55 seconds inside the function and 30.13 seconds dispatch-to-result. All four paid calls completed; all cloud apps are stopped. No neural training was performed. The shared MNIST environment’s metered snapshot rose from $3.97677 to $4.07871, an increase of about $0.10. Snapshot checked 2026-09-09T23:27:08.442662+00:00; this is metering, not a final invoice.

The original $30 cap still applies. Immutable worst-case reservations rose from $23.10357 to $23.88100, including $0.77743 for these four 180-second A100 allocations plus startup/idle allowances. Old reservations were not released or reset. Reservations and actual metering are different quantities.

Billing snapshot · Shared reservation ledger · Stopped-app check

Reproduce without new compute

From the repository root, use the existing Python environment with NumPy, PyTorch and scikit-learn. The stored policy manifest is immutable: evaluation verifies its validation data and source hashes before reading test arrays. The CPU full-width qualification used 32 original validation examples only to check API/runtime; its outputs are excluded from the experiment.

experiments/.venv/bin/python experiments/ciresan_stochastic_depth/layerdrop_hypotheses/analyze.py \
  --phase evaluate \
  --reference-dir experiments/ciresan_stochastic_depth/results/hypotheses/source-results
experiments/.venv/bin/python experiments/ciresan_stochastic_depth/layerdrop_hypotheses/export_report.py --ready
python3 scripts/build_mnist_layerdrop_report.py
node experiments/ciresan_stochastic_depth/layerdrop_hypotheses/test_page.cjs

Frozen experimental protocol · Pre-audit hashes/specifications · Frozen policies · Full analysis · Independent verification

Fable’s argument: mathematical audit · Executed counterexamples