Decision and Meta-Review
accepted
Decision note: Accepted: its area chair recommended acceptance and the program chair accepted it.
Originality: not checked (the PC's call, applied at publication)
Input-embedding rows receive a gradient only when their token occurs, and Adam(W)'s effect on such a row is known only through a one-step bound and an unsaturated frequency scaling. For a row occurring with probability per step we split its per-occurrence path into an exact and an approximate part. The exact part is a cap on rare-row steps, from Adam's update with empty moments, and a truncation of the momentum trail by the next occurrence, exact under i.i.d. occurrences; it makes , not token frequency, the batch variable. The approximate part, a residual second-moment factor resting on three closures, adds a knee at and a decay equilibrium proportional to ; trained models do not confirm it. In GPT models trained on FineWeb, the rare-row path is within [0.972, 1.014] of the prediction at (at only on rows seen three or four times), which checks the cap's assumptions, not the closures; at no row is rare enough. Binned in , batch sizes lie several times closer than binned in frequency. With no fitted parameter, the full expression has a higher pooled log- than every null we scored at batch sizes up to 32, by as little as 0.026, but not at 128; no scored null pairs the cap with a fitted decline. The knee is fitted beyond in 9 of 10 cells, decayed norm scales as , and occurrence-gated decay shows no resolvable effect.
Figure 1. With no free parameter, Prop. 2 fits the per-occurrence path of GPT input-embedding rows better than every null law we scored in 8 of 10 Adam cells. Bars are log-space against the constant law, mean over 3 training seeds, for each training cell (table 2 gives the intervals); the label above each group is Prop. 2 minus the better of the two plotted nulls. At (L07, L08) the uncapped null wins. No scored null pairs the cap with a fitted decline.
Introduction
Language models are trained with ever larger vocabularies (Tao et al., 2024; Kaplan et al., 2020), and most of their input-embedding rows, like the word vectors before them (Mikolov et al., 2013), are trained on a small fraction of steps: a row receives a gradient only when its token appears in the batch, and is exactly untouched otherwise. Adam and its decoupled-decay variant AdamW (Kingma et al., 2015; Loshchilov et al., 2019) are the default optimizers for such models, and practitioners set their parameters for these rows largely by recipe: a second-moment decay for stability (Wortsman et al., 2024; Molybog et al., 2023), or no weight decay on embeddings at all (OLMo et al., 2025). Rare-token embeddings are known to degenerate and to separate from frequent ones (Gao et al., 2019; Gong et al., 2018), and the same sparsity governs the ID tables of recommender models (Naumov et al., 2019). How Adam treats a row that is rarely updated decides how fast rare tokens learn and how far their embeddings shrink under decay, and it is known only qualitatively.
The qualitative picture is consistent across several lines of work. Adam helps rare classes relative to gradient descent (Kunstner et al., 2024), and its advantage on transformers has been traced to sign-like behaviour (Kunstner et al., 2023) and to heterogeneous curvature (Zhang et al., 2024); its per-row normalization correlates with token frequency (Li et al., 2022) and is held responsible for anisotropic rare-word embeddings (Stollenwerk et al., 2025); weight decay degrades low-frequency tokens (Pinto et al., 2024); and at the output layer, adaptive normalization biases the fixed point of rare-token logits (Kar, 2026). However, none of these gives the step a rare input row actually takes. The one quantitative statement, Kingma and Ba's bound for severe sparsity (Kingma et al., 2015), covers the occurrence step and not the momentum trail that follows it, and the frequency-scaling reading implies an inverse-square-root growth of the step that never saturates (Li et al., 2022; Stollenwerk et al., 2025). Without a law there is no way to predict from token counts which rows Adam caps, how a change of or batch size rescales them, or how much decoupled decay starves them, and no way to test such a prediction row by row.
We derive the step of a Bernoulli-gated row. The derivation separates two factors. The truncation of the momentum trail by the next occurrence is exact under i.i.d. occurrences, by a renewal–reward identity. The effect of the residual second moment rests on three named closures, and the dropped residual momentum predicts where the law must fail. Together they give the per-occurrence path in terms of the per-step occurrence probability , with a cap set by alone, a decline above a knee at , a batch-size collapse in , and a decay equilibrium proportional to that occurrence-gated decay (OG-WD) removes. We test it in an exact scalar model, where its assumptions hold by construction, and on every input-embedding row of GPT models trained on FineWeb, against null laws (uncapped, SGD-like, the one-step bound, the constant law) and an SGD control that removes the mechanism. The cap and the truncation are the result we stand behind; the residual factor, and with it the knee and the decay equilibrium, is a closure-based approximation that the trained models do not confirm.
In the exact model, the law is within 5.3% (largest upper bound) of the measured path of rare rows in all 48 configurations, and each of its two factors is needed in all but one configuration. In the trained models, the measured rare-row path lies within [0.972, 1.014] of the prediction at , for two model widths and three batch sizes over 3 training seeds. Lemma 1 implies this agreement once A1, A4 and A5 hold, so it tests those assumptions in a real run, not the closures. The tests that need the theory beyond Lemma 1 are mixed: with no free parameter the law has a higher pooled log- than every null we scored at (table 2), though no scored null pairs the cap with a fitted decline, and binning in collapses batch sizes where frequency does not; but it under-predicts dense rows, loses to a fitted uncapped law at , and its free knee, its decay equilibrium and the norm-versus- slope of decayed rows do not meet their pre-registered tolerances. Our test of OG-WD could not resolve its effect on training. Our key contribution is the exact part of the per-occurrence path of sparsely updated Adam rows, the cap and the trail truncation, with as the batch variable, together with a row-level test in trained language models that confirms the cap where the rare region is reached () and shows where the closure-based residual factor fails.
Related Work
Adam's normalization, sign descent and weight decay. Adam combines bias-corrected moving averages of the gradient and its square (Kingma et al., 2015), and its single-step bound under severe sparsity is the term of the trail we sum. Dissecting Adam into a sign direction and a variance-adaptive magnitude explains when sign-like updates help (Balles et al., 2018), sign descent has its own convergence theory (Bernstein et al., 2018), and the gap between SGD and Adam on transformers tracks sign descent more than gradient noise (Kunstner et al., 2023); heavy-tailed class imbalance shows why that matters for rare classes in language models (Kunstner et al., 2024). Sign-based optimizers found by search keep only the sign of a momentum (Chen et al., 2023). The variance of Adam's early second moment motivates warmup and rectification (Liu et al., 2019), and a short second-moment memory lets rare large gradients be forgotten, which breaks convergence and motivates AMSGrad (Reddi et al., 2018), and small second moments are blamed for loss spikes at scale (Molybog et al., 2023; Wortsman et al., 2024; Wortsman et al., 2023). Recent scaling studies find that must rise as the batch shrinks (Porian et al., 2024; Marek et al., 2025), a dense-gradient analogue of the and dependence derived here. On the decay side, decoupling the shrink from the gradient defines AdamW (Loshchilov et al., 2019); with it, weight norms reach a rotational equilibrium in which growth balances decay (Kosson et al., 2024), and the weights act as a moving average with timescale , which sets how should scale (Wang et al., 2025). Memory-saving and layer-wise variants change the second moment's form (Shazeer et al., 2018; You et al., 2019), quantized optimizers single out the embedding layer for special treatment (Dettmers et al., 2021), and weight decay in modern training acts mainly through optimization dynamics (D'Angelo et al., 2023). Batch size enters through the gradient noise scale (McCandlish et al., 2018; Smith et al., 2017), SDE limits of adaptive methods give scaling rules for dense coordinates (Malladi et al., 2022), and hyperparameter-transfer schemes rescale per-layer learning rates with width (Yang et al., 2022). All of these treat a parameter that receives a gradient on every step. We study the row that does not: its Adam step becomes per-occurrence sign descent with a cap fixed by , its relevant batch variable is rather than the noise scale, and its decay equilibrium carries a factor that the dense analyses do not have.
Rare tokens and frequency-dependent optimization. A second line studies rare tokens directly. Frequency-aware SGD sets per-token learning rates by frequency and proves gains over plain SGD, reading Adam's second moment as an approximately inverse-square-root frequency scaling (Li et al., 2022). Coupled Adam attributes anisotropic embeddings to that per-row scaling and shares the second moment across the vocabulary (Stollenwerk et al., 2025). Empirically, stronger weight decay hurts low-frequency tokens disproportionately across model sizes (Pinto et al., 2024), and the OLMo 2 recipe removes embedding decay to keep embedding norms healthy (OLMo et al., 2025). Earlier work on word representations found rare-word embeddings clustered apart from frequent ones and corrected them adversarially or by regularization (Gong et al., 2018; Gao et al., 2019). The closest theory analyzes the softmax output layer, where "a rare token receives a small positive logit gradient on most steps and a much larger negative gradient on the few steps when it is the target", and shows that Adam-like normalization shifts the fixed point of rare logits below their frequency, in closed form for RMSProp with periodic arrivals (Kar, 2026). Its ratio of the mean gap to the second-moment timescale is, in our notation, about , but its object is a logit fixed point under gradients that never vanish; ours is the input side, whose gradient is exactly zero between occurrences, and the step path such a row takes, so the results complement each other. Against this line we supply what it lacks: a quantitative step law with a saturation that the inverse-square-root reading misses, a predicted knee that moves with , a collapse across batch sizes, a decay mechanism for the frequency effect, and a row-level test in trained models with null laws taken from these works.
Method
Figure 2. The occurrence law. What enters, what Adam does to it, what is measured.
In this section, we derive the occurrence law and the quantities we test it on; figure 2 sketches the chain from a gated gradient to the measured path. Section 3 sets up a Bernoulli-gated row under AdamW and defines the per-occurrence path. Section 3 derives the law, separating the factor that is exact from the one that rests on closures, followed by section 3 on decoupled decay and its occurrence-gated variant, and section 3 on the estimators and intervals the experiments report.
A Row That Is Rarely Updated
Consider an input-embedding table with rows after step . Let indicate that token occurs in the batch of step , with its per-step occurrence probability. A row's gradient is , where is the gradient given occurrence: for an untied input embedding it is exactly zero on every step the token is absent (assumption A1). We also assume that occurrences are i.i.d. across steps and independent of the past (A2), which our sampler satisfies by construction because each step draws its windows uniformly at random with replacement, and that the law of the state at an occurrence is stationary (A3), which holds only approximately in a network whose gradients shrink as it trains. The same structure arises in recommender ID tables and other sparsely indexed parameters (Li et al., 2022). Per coordinate and with the row index dropped, AdamW (Kingma et al., 2015; Loshchilov et al., 2019) updates the row as
where and are the first and second moments, is the Adam direction (the step divided by its learning rate ), and is the decoupled decay multiplier with weight decay . Equation 1 is the update our code applies to every embedding row, so the direction is logged exactly rather than recovered by differencing weights.
The quantity we predict is how far a row travels per occurrence, including the momentum trail it leaves on the steps where it is absent. We define the per-occurrence path as
where counts the occurrence steps up to . Dividing by makes a root-mean-square per coordinate, and using rather than makes it free of the learning-rate schedule. Equation 2 is a path, not a displacement; for an isolated occurrence the two coincide, and we log both.
The Occurrence Law
The trail is exact. Kingma and Ba bound the single step of an occurrence under severe sparsity (Kingma et al., 2015), and sign-based readings of Adam treat its direction as for dense gradients (Balles et al., 2018; Kunstner et al., 2024). Neither follows what happens after the occurrence. On a step with , equation 1 gives and , so with bias correction and negligible (A4, A5; A4 fails early in training at ) the direction shrinks by a common factor and keeps its orientation. Summing that geometric trail between an occurrence at step and the next one, a gap later, and applying the renewal–reward theorem under A1–A3 gives
where is the expectation over the state at an occurrence and . The factorization uses only A2: the gap depends on future occurrences, which are independent of . The truncation factor is therefore exact whenever occurrences are i.i.d. across steps, and nothing in equation 3 is mean-field. If the moments are empty before an occurrence, for every coordinate, so a rare row performs sign descent (Bernstein et al., 2018) with a step independent of (Lemma 1); summing its trail gives the cap .
The residual second moment is the one approximation. At an occurrence, depends on the residual moments and left by earlier occurrences. Three closures make a function of alone: the residual momentum is dropped (M1), is replaced by its stationary mean (M2, exact in mean under A2–A3, with a Jensen gap of known sign), and each coordinate is set to its rms (M3). Combined with equation 3 they give Proposition 2, the occurrence law:
where is the rare-row constant (5.84, 10.47 and 31.77 for and ), is the exact truncation factor and the residual factor that rests on M1–M3. Three regimes follow. As , , the cap. For the law decays as , which is the regime that frequency-scaled rates describe (Li et al., 2022; Stollenwerk et al., 2025). The knee between them sits at , where (0.0526, 0.0101 and 0.0010 for the three ). Equation 4 is also the decomposition we test: the ablated predictors set , , or both (the cap alone).
Where the law stops. Closure M1 fails for dense rows. At with i.i.d. zero-mean noise of variance , the momentum has stationary variance while as , so
where the ratio of the two, , is the momentum that M1 discarded. Equation 5 predicts the sign and the size of Prop. 2's error for frequent rows, and with it the scope of every claim below: equation 4 is a law for rows at or below the knee and in the knee region, and is not a law for dense rows. For M1 is exact and only the M2 and M3 closures remain.
Batch size and . Because equation 4 depends on the data only through , curves of against the measured should coincide across batch sizes, while curves against token frequency should shift, since for sequences of length when positions are independent (Corollary 4). Real text is bursty, so this map is only approximate, and our collapse test uses directly. The noise-scale view of batch size (McCandlish et al., 2018; Smith et al., 2017) does not apply to such rows, because enlarging the batch changes how often a row is updated before it changes the noise in its gradient; dense-gradient studies that couple to batch size (Porian et al., 2024; Marek et al., 2025) meet the same variable from the other side. Below the knee and at fixed , raising multiplies a rare row's per-occurrence step by the ratio of the constants while leaving frequent rows nearly unchanged (Corollary 5). This may contribute to the folklore choice of for stability (Wortsman et al., 2024; Molybog et al., 2023), and it is how rare large updates enter convergence counterexamples (Reddi et al., 2018); we do not test the stability link here.
Decoupled Decay and Occurrence-Gated Decay
The problem with decaying every row. AdamW shrinks every row on every step (Loshchilov et al., 2019), whereas a rare row receives updates on a fraction of them. Equilibrium analyses of weight decay assume a parameter group updated on every step (Kosson et al., 2024; Wang et al., 2025). For a row we define the per-step diffusion ; its limits are as , by Lemma 1 with symmetric noise, and 1 at , and we interpolate between them with , a heuristic. Assuming symmetric gradient noise (A7), which the coherent gradients of a trained network violate, and treating increments as uncorrelated beyond the trail's correlation time (A8), and taking constant and gives Proposition 3:
where is the initial row and . Below the knee the equilibrium norm is therefore proportional to : AdamW starves rare rows, the effect reported empirically for low-frequency tokens (Pinto et al., 2024) and avoided in practice by removing embedding decay (OLMo et al., 2025).
What gating changes. Occurrence-gated decay (OG-WD) decays a row only on the steps it occurs, , and leaves the Adam step unchanged. To first order the same calculation gives
where the limit is taken after . The equilibrium no longer depends on below the knee, and frequent rows () are decayed exactly as under AdamW. The price is the timescale , which for a rare row is longer by the factor ; equation 7 therefore also predicts that a short run measures the transient, in which OG-WD behaves like no decay. We compare OG-WD against AdamW, no embedding decay, and lazy Adam rows, whose moments, decay and parameter change only on occurrence steps.
Estimators and Intervals
Per-row estimates. Each run logs, for every row, its occurrence count and summed path , giving and . Only rows with enter. In the rare limit each occurrence contributes the deterministic amount , so the per-row estimate is nearly noise-free exactly where the main claim lives, which is why rare-bin intervals are narrow. A ratio is summarized by its median over the rows of a region or bin.
Comparing laws and runs. Each candidate law is scored against the constant law in log space, and every per-run statistic receives an interval over the training seeds:
where is the run's median path, and are the mean and standard deviation of over seeds, and . Prop. 2, the cap alone and the one-step bound enter the left part of equation 8 with no free parameter; the uncapped law implied by frequency-scaled analyses (Stollenwerk et al., 2025; Li et al., 2022) and the SGD-like law receive their best log-space scale, which favours them. The right part of equation 8 is the interval reported for every number in section 4; with three seeds it is wide, and its coverage rests on normality across seeds, which three values cannot check.
Experiments
Experimental Setup
Table 1. Data behind each test. Sizes of each source. The training shards are used whole; the validation shard is read through fixed random subsamples (see text).
| Source | FineWeb train | FineWeb val | Scalar model |
|---|---|---|---|
| Size | 400000000 tokens | 100000000 tokens | 48 configs |
| Unit | 1024-token windows | 1024-token windows | 4000 coords 30 |
| Synthetic | ✗ | ✗ | ✓ |
| Used whole | ✓ | ✗ | ✓ |
Implementation Details. Two testbeds probe the law (table 1). The exact scalar model is synthetic by design: it runs the update of equation 1 on Bernoulli-gated coordinates, where assumptions A1–A3 hold exactly, so any error it shows belongs to the closures and not to a trained network. Its 48 configurations cross Gaussian, Student- and signal-plus-noise gradients (, ) with and , plus and variants (section 6), each over 30 values of for 40000 steps and 3 seeds. The language-model testbed trains GPT models with untied input embeddings on the GPT-2 tokenization of FineWeb (Penedo et al., 2024): all four training shards (400000000 tokens) are used whole, each step draws windows of 1024 tokens uniformly with replacement, and the validation shard is evaluated once, at the end of each run. Embedding rows follow equation 1 exactly as written (Loshchilov et al., 2019); the body uses fused AdamW, and , throughout.
Compared configurations. Training cells L01–L08 cross with at (8 layers, learning rate , 4000 steps; 2000 steps at ); S01–S02 repeat and at (12 layers, learning rate ); L09 replaces the embedding's Adam by SGD with momentum, the control that removes the mechanism. Cells D01–D04 run 6000 steps at learning rate with embedding decay on every row (AdamW, D01), no embedding decay (D02), OG-WD (D03) and lazy Adam rows (D04). Every cell has 3 training seeds that redraw initialization and data order, 45 runs in all; every hyperparameter was fixed in the plan before any run, and no configuration was selected on validation or any other data. Intervals are 95% -intervals over seeds (right part of equation 8); proportions carry Wilson intervals. Section 6 lists every metric, the run history and where each result is stored.
The Law in GPT Input Embeddings
This family asks whether the law predicts rows of a trained network with no parameter fitted to it.
Table 2. Log-space of each step law against the constant law (), per training cell. Each entry scores the measured per-occurrence path of every input-embedding row with at least 3 occurrences (equation 8); is the constant law. Prop. 2, Lemma 1 and the one-step bound have no free parameter; the uncapped and SGD-like nulls get their best scale. Mean over 3 training seeds, with the 95% -interval beneath. The row is Prop. 2 minus the best null of each run (uncapped, SGD-like, one-step or constant), averaged over seeds. Scores pool all , mostly above at ; no null pairs the cap with a fitted decline.
| Step law | L01, | L03, | L07, | L05, | L04, | L08, |
| SGD-like, | 0.217 | 0.073 | -0.425 | 0.005 | -0.070 | -0.480 |
| [0.202, 0.232] | [0.065, 0.082] | [-0.439, -0.411] | [-0.006, 0.017] | [-0.078, -0.062] | [-0.519, -0.440] | |
| [1pt] One-step bound (Kingma–Ba) | -9.085 | -2.742 | -0.523 | -0.501 | -0.217 | -2.209 |
| [-9.095, -9.074] | [-2.744, -2.739] | [-0.525, -0.520] | [-0.502, -0.499] | [-0.245, -0.190] | [-2.255, -2.163] | |
| [1pt] Cap alone (Lemma 1) | -0.731 | -2.124 | -6.445 | -3.688 | -8.575 | -17.355 |
| [-0.736, -0.726] | [-2.126, -2.122] | [-6.465, -6.426] | [-3.697, -3.678] | [-8.699, -8.451] | [-17.628, -17.082] | |
| [1pt] Uncapped, | 0.843 | 0.893 | 0.858 | 0.891 | 0.874 | 0.833 |
| [0.837, 0.848] | [0.893, 0.894] | [0.858, 0.858] | [0.891, 0.891] | [0.872, 0.877] | [0.829, 0.838] | |
| [1pt] Prop. 2, | 0.965 | 0.922 | 0.732 | 0.929 | 0.938 | 0.714 |
| [0.964, 0.965] | [0.921, 0.922] | [0.732, 0.733] | [0.929, 0.929] | [0.934, 0.942] | [0.711, 0.718] | |
| [1pt] (Prop. 2 best null) | 0.122 | 0.028 | -0.125 | 0.038 | 0.063 | -0.119 |
| [0.116, 0.128] | [0.027, 0.029] | [-0.126, -0.125] | [0.038, 0.039] | [0.058, 0.069] | [-0.127, -0.111] |
As shown in table 2 and, for all cells, table 7, Prop. 2 has the highest log- of the five laws in every cell with , and its margin over the best null is above 0 in all 8 such cells, 0.052 on average (-interval over the 8 cells [0.025, 0.079]). The cap alone and the one-step bound, which ignore the decline above the knee, score below the constant law. At the uncapped null wins: Prop. 2's margin is -0.122 (interval over the two cells [-0.162, -0.082]); given its best scale, Prop. 2's shape recovers 0.893 and 0.898 there, so the misfit lies in the absolute level of frequent rows, where equation 5 already predicts an under-estimate. Two limits bound this comparison. First, no scored null pairs the cap with a decline: the uncapped null lacks the cap, and the cap alone and cap times truncation (, log- -4.170 in L04) lack the decline. The fair competitor, a capped power law with one fitted scale, was not scored and may tie at , so the table shows that a cap and a decline are both needed, not that the closures' shape beats it. Second, the score pools every row with : in the row files almost every scored row lies above at , and most do at and at , so those cells score the decline and the dense rows of equation 5, not the rare regime, whose test is the ratio below. Figure 1 shows the same comparison for all ten Adam cells.
Table 3. Measured over predicted per-occurrence path of rare embedding rows (target 1). Rare region: rows with ; the entry is the per-run median ratio over those rows, and Rare rows is their mean number per run. Only rows with at least 3 occurrences enter, so at , where is just above four, the rare region holds only rows seen three or four times. Lowest bin: the rarest bin with rows (for L08, run for 2000 steps, it lies above ). Max step: the largest per-occurrence step of any row divided by . Mean over 3 training seeds, 95% -interval in brackets. "–": at , lies below the smallest a row with 3 occurrences can have in 4000 steps.
| Cell | Rare rows | Rare / Prop. 2 | Rare / Lemma 1 | Lowest bin / Prop. 2 | Max step / | |||
|---|---|---|---|---|---|---|---|---|
| L01 | 0.950 | 8 | 512 | 6185 | 0.997 [0.994, 1.000] | 0.925 [0.923, 0.928] | 1.011 [1.010, 1.012] | 1.025 [0.996, 1.054] |
| L03 | 0.950 | 32 | 512 | 1336 | 0.996 [0.992, 1.000] | 0.929 [0.927, 0.931] | 1.005 [1.005, 1.006] | 1.002 [0.991, 1.013] |
| L07 | 0.950 | 128 | 512 | 364 | 0.995 [0.983, 1.008] | 0.927 [0.912, 0.942] | 1.003 [0.984, 1.021] | 1.001 [0.989, 1.013] |
| S01 | 0.950 | 32 | 768 | 1336 | 0.995 [0.991, 0.998] | 0.928 [0.925, 0.931] | 1.004 [1.003, 1.006] | 1.001 [0.994, 1.008] |
| L02 | 0.990 | 8 | 512 | 527 | 0.993 [0.972, 1.014] | 0.944 [0.926, 0.962] | 1.002 [0.978, 1.025] | 1.000 [0.999, 1.000] |
| L05 | 0.990 | 32 | 512 | 163 | 0.989 [0.983, 0.994] | 0.940 [0.937, 0.943] | 0.992 [0.980, 1.003] | 1.000 [0.999, 1.000] |
| L06 | 0.999 | 8 | 512 | 0 | – | – | 0.897 [0.859, 0.936] | 0.985 [0.975, 0.995] |
| L04 | 0.999 | 32 | 512 | 0 | – | – | 0.878 [0.839, 0.918] | 0.982 [0.969, 0.996] |
| L08 | 0.999 | 128 | 512 | 0 | – | – | 0.871 [0.792, 0.950] | 0.915 [0.907, 0.924] |
| S02 | 0.999 | 32 | 768 | 0 | – | – | 0.889 [0.825, 0.954] | 0.980 [0.963, 0.996] |
At the rare cap transfers. In every cell with , both sizes and all three batch sizes, the measured rare-row path lies within [0.972, 1.014] of Prop. 2 (table 3), against the pre-registered band [0.9, 1.1]; the cap alone over-predicts it (ratios 0.925–0.944), as equation 4 predicts at . This tests Lemma 1's assumptions A1, A4 and A5 (e.g. a bias correction not yet decayed would break it), not the closures. At the rare rows are few and seen three or four times, so their is coarse (section 6). The cap bounds the largest per-occurrence step only to within its intervals: the cell means span 0.915–1.025, and the largest upper end is 1.054 (L01, whose mean exceeds the cap). At the rare region is out of reach, so the cap is not testable there; the lowest bin reached (above for L08, which runs 2000 steps) sits at 0.871–0.897 of Prop. 2, with every interval reaching below the band. The SGD control behaves as the law requires: in L09 the SGD-like null fits best (0.562 [0.555, 0.570]) and Prop. 2's shape fits worse than a constant (-0.565), so the Adam-cell fit is not a property of token frequency alone.
Table 4. Largest gap between batch sizes of the binned median path (). Gap: of the bin medians, over bins with at least 20 rows at every , binned in measured or in token frequency . Mean over 3 training seeds, 95% -interval in brackets. Last column: lower end of the -gap interval divided by the upper end of the -gap interval.
| Batch sizes | Gap in | Gap in | -gap low / -gap high | |
|---|---|---|---|---|
| 0.950 | 8, 32, 128 | 0.063 [0.058, 0.069] | 1.657 [1.653, 1.660] | 24.0 |
| 0.990 | 8, 32 | 0.045 [0.039, 0.051] | 0.932 [0.931, 0.934] | 18.4 |
| 0.999 | 8, 32, 128 | 0.145 [0.078, 0.212] | 1.677 [1.639, 1.715] | 7.7 |
Corollary 4 holds in its comparative form (table 4): binned in , the curves of different batch sizes differ by 4.5–14.5%, while binned in token frequency they differ by 93–168%, at least 7.7 times more at every . The pre-registered absolute threshold of 5% fails: its interval contains 5% at and lies above it elsewhere. The free knee fails too: its fitted position exceeds twice in 9 of 10 Adam cells.
The Exact Scalar Model
This family isolates the closures M1–M3 from everything a network adds.
Table 5. Error of the occurrence law in the exact scalar model (), by gradient noise. Top block: largest in percent over the configurations of each noise family (seed mean), with the largest upper end of the 95% -interval over 3 MC seeds in parentheses. Rare region: ; burn-in: steps. Bottom block: configurations in which dropping one factor of equation 4 makes the worst- error at least twice that of Prop. 2, counting only those whose conservative bound clears 2 (no-truncation is identical to Prop. 2 at and is counted at only).
| Quantity | Gaussian | Student- | signal, | signal, |
|---|---|---|---|---|
| Prop. 2, rare region, all steps | 3.5 (5.3) | 3.9 (4.6) | 3.4 (4.6) | 3.2 (4.6) |
| Prop. 2, rare region, after burn-in | 2.2 (3.7) | 2.5 (3.4) | 2.0 (2.6) | 2.9 (3.0) |
| Lemma 1 cap alone, rare region | 18.7 (18.8) | 19.0 (19.2) | 17.9 (17.9) | 16.2 (16.4) |
| Prop. 2, worst on the whole grid | 125.9 (125.9) | 120.7 (120.8) | 389.1 (389.4) | 624.0 (624.1) |
| No truncation (), | 16/16 | 4/4 | 4/4 | 4/4 |
| No residual () | 24/24 | 8/8 | 8/8 | 7/8 |
In the rare region Prop. 2 is within 3.9% in all 48 configurations, largest upper bound 5.3%, and within 2.9% after burn-in (table 5). Over the whole grid Prop. 2 fails: for Gaussian noise the worst error is 125.9%, reached at , and 16 of 24 Gaussian configurations lie wholly above 15%, which is the residual momentum of equation 5. Both factors are needed, and the decay equilibrium of equation 6 is not confirmed to 15% (section 6).
Decay of Rare Rows
This family tests the one consequence the law suggests for training: whether gating decay by occurrence helps rare tokens.
Table 6. Loss after rare tokens, each decay arm minus AdamW, in nats ( favours the arm). Paired by training seed and evaluation window; columns are the three rarest token-frequency buckets and the validation loss. Mean over 3 training seeds, 95% -interval in brackets. Pass: buckets among the three rarest in which both this interval and the window bootstrap lie below 0 (the pre-registered test needs 2). Slope: OLS slope of on for rows below .
| Embedding arm | val | Pass | Norm slope | |||
|---|---|---|---|---|---|---|
| No embedding decay | -0.501 [-3.061, 2.060] | -0.506 [-2.453, 1.442] | -0.339 [-1.752, 1.075] | -0.160 [-1.055, 0.735] | 0/3 | 0.718 [0.713, 0.722] |
| OG-WD (gated decay) | -0.348 [-1.620, 0.924] | -0.481 [-1.961, 0.998] | -0.368 [-1.579, 0.843] | -0.185 [-0.927, 0.558] | 0/3 | 0.708 [0.705, 0.710] |
| lazy Adam rows | -0.116 [-2.405, 2.173] | -0.310 [-2.075, 1.455] | -0.303 [-1.573, 0.968] | -0.169 [-0.935, 0.596] | 0/3 | 0.552 [0.550, 0.554] |
| AdamW (reference) | – | – | – | – | – | 0.787 [0.757, 0.816] |
The pre-registered test is null for every arm (table 6): no arm lowers the loss after rare tokens in any of the three rarest buckets once the seed interval is required, and every interval contains 0. The negative means come from one late-destabilizing AdamW run (section 6). The norm law is contradicted in both arms. Under AdamW the norm-versus- slope is 0.787 [0.757, 0.816], excluding the predicted 1 although this run is long enough for the AdamW equilibrium; noise in explains little of the gap, and the coherent gradient component that violates A7 is a candidate we have not measured. Under OG-WD the slope is 0.708, not 0 but close to no decay (0.718), as equation 7 predicts for a short run: at the OG-WD timescale far exceeds the 6000 steps run, so the OG-WD runs measure its transient, not its equilibrium. No run diverged (0 of 45, Wilson upper bound 0.079).
Conclusion
We derived the per-occurrence step of Adam(W) rows that receive a gradient on a fraction of steps, and tested it in an exact scalar model and on the input embeddings of GPT models trained on FineWeb. Ranked by how much theory beyond Lemma 1 each prediction uses, the cap uses none and holds wherever the rare region is reached (; at on rows seen three or four times), which confirms A1, A4 and A5 in a real run. The comparative batch collapse uses only that is the right variable, and holds. The parameter-free fit over all rows uses the truncation and the closures, their only support in trained models: it beats every null we scored at by 0.052 on average but by as little as 0.026 in one cell, and loses at . The predictions that rest most on the closures and on Proposition 3 are unconfirmed: the knee position (fitted beyond in 9 of 10 cells), the absolute 5% collapse threshold, the decay equilibrium, the norm-versus- slope (0.787, not 1), and dense rows. The OG-WD arm and were not resolved. What stands is therefore the exact cap and truncation and as the batch variable; the residual factor is an approximation the trained models do not confirm.
Limitations. (i) The fit comparison lacks its fair competitor, a capped power law with one fitted scale; until it is scored, the log- margin shows that a cap and a decline are needed, not that the closures' shape is right. (ii) The log- pools all rows with , mostly above at or ; no score restricted to the stated scope is reported. (iii) The cap is confirmed only at , in models of width at most 768 trained for 2000 to 6000 steps on GPUs shared with other jobs, an early slice of training. Two questions follow directly: runs long enough to reach the rare region at and the OG-WD equilibrium timescale, and vocabularies or ID tables large enough that most rows sit below the knee.
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Appendix
Protocol, Run Record and Complete Results
Table 7. Every training cell: log-space of three laws, the margin over the best null, and validation loss. Mean over 3 training seeds, 95% -interval in brackets. L09 trains the embedding with SGD and momentum, so Prop. 2's absolute level has no meaning there; D04 updates rows lazily, with the same consequence. D01–D04 use learning rate and 6000 steps.
| Cell | Prop. 2 | uncapped | SGD-like | vs. best null | Val loss (nats) | |||
|---|---|---|---|---|---|---|---|---|
| L01 | 0.950 | 8 | 512 | 0.965 [0.964, 0.965] | 0.843 [0.837, 0.848] | 0.217 [0.202, 0.232] | 0.122 [0.116, 0.128] | 5.324 [5.299, 5.348] |
| L03 | 0.950 | 32 | 512 | 0.922 [0.921, 0.922] | 0.893 [0.893, 0.894] | 0.073 [0.065, 0.082] | 0.028 [0.027, 0.029] | 4.472 [4.462, 4.482] |
| L07 | 0.950 | 128 | 512 | 0.732 [0.732, 0.733] | 0.858 [0.858, 0.858] | -0.425 [-0.439, -0.411] | -0.125 [-0.126, -0.125] | 4.240 [4.219, 4.261] |
| S01 | 0.950 | 32 | 768 | 0.922 [0.921, 0.922] | 0.893 [0.893, 0.894] | 0.067 [0.054, 0.080] | 0.028 [0.028, 0.029] | 4.356 [4.350, 4.362] |
| L02 | 0.990 | 8 | 512 | 0.965 [0.965, 0.965] | 0.919 [0.916, 0.921] | 0.148 [0.138, 0.158] | 0.047 [0.044, 0.049] | 5.153 [5.137, 5.170] |
| L05 | 0.990 | 32 | 512 | 0.929 [0.929, 0.929] | 0.891 [0.891, 0.891] | 0.005 [-0.006, 0.017] | 0.038 [0.038, 0.039] | 4.389 [4.361, 4.417] |
| L06 | 0.999 | 8 | 512 | 0.946 [0.938, 0.954] | 0.920 [0.914, 0.927] | -0.015 [-0.127, 0.097] | 0.026 [0.023, 0.029] | 5.553 [5.039, 6.067] |
| L04 | 0.999 | 32 | 512 | 0.938 [0.934, 0.942] | 0.874 [0.872, 0.877] | -0.070 [-0.078, -0.062] | 0.063 [0.058, 0.069] | 4.378 [4.370, 4.385] |
| L08 | 0.999 | 128 | 512 | 0.714 [0.711, 0.718] | 0.833 [0.829, 0.838] | -0.480 [-0.519, -0.440] | -0.119 [-0.127, -0.111] | 4.189 [4.173, 4.205] |
| S02 | 0.999 | 32 | 768 | 0.939 [0.933, 0.944] | 0.874 [0.872, 0.876] | -0.065 [-0.083, -0.047] | 0.064 [0.059, 0.070] | 4.315 [4.160, 4.471] |
| L09 | 0.950 | 32 | 512 | -252.842 [-256.620, -249.063] | 0.502 [0.479, 0.525] | 0.562 [0.555, 0.570] | -253.404 [-257.175, -249.633] | 4.585 [4.581, 4.590] |
| D01 | 0.950 | 32 | 512 | 0.930 [0.909, 0.950] | 0.888 [0.884, 0.893] | 0.027 [-0.520, 0.574] | 0.041 [0.016, 0.066] | 4.607 [3.829, 5.386] |
| D02 | 0.950 | 32 | 512 | 0.925 [0.923, 0.927] | 0.890 [0.889, 0.891] | 0.127 [0.098, 0.157] | 0.036 [0.033, 0.039] | 4.448 [4.261, 4.634] |
| D03 | 0.950 | 32 | 512 | 0.925 [0.924, 0.925] | 0.890 [0.889, 0.890] | 0.036 [0.023, 0.049] | 0.035 [0.034, 0.035] | 4.423 [4.386, 4.459] |
| D04 | 0.950 | 32 | 512 | -200.637 [-209.627, -191.648] | -11.661 [-12.631, -10.691] | -4.071 [-4.486, -3.657] | -200.637 [-209.627, -191.648] | 4.438 [4.423, 4.453] |
Data and benchmarks. The language-model data are the GPT-2-tokenized FineWeb shards: four training shards of 400000000 tokens in all, used whole, and one validation shard of 100000000 tokens. The training data are not subsampled; each step samples windows uniformly at random with replacement from all training shards, so the largest run (, 2000 steps) sees overlapping windows at random but never cycles through the data in order. The validation shard is subsampled: the validation loss is computed once per run, after training, on 64 fixed batches of 32 windows drawn uniformly with a fixed seed (128 batches for D01–D04), the same windows in every run; the loss after rare tokens is the next-token loss on validation-shard windows of 255 context tokens whose last input token has its training-shard frequency in a given bucket, up to 8192 windows per bucket, the same windows for every arm and seed. There is no separate test split and nothing was tuned, so the validation shard plays the role of a test set that is read once per run. Benchmarks considered: FineWeb, OpenWebText, TinyStories and a recommender ID table. FineWeb was used because its Zipfian vocabulary spreads rows over the whole range of table 3 at these batch sizes and its shards were already prepared; OpenWebText would have tested the same question on similar web text at extra preparation cost; TinyStories uses too few distinct tokens for a rare-row study, and an ID table would have added a second domain outside the plan. The scalar model's block uses Gaussian noise, and its decay block () Gaussian noise with . The scalar Monte Carlo data are synthetic: they are the only setting in which A1–A3 hold exactly, which is what isolates the closures.
Metrics computed. Per row: , the path , the net displacement, the largest single and per-occurrence steps, and the final norm. Per run: the median ratio of measured to predicted path for Prop. 2, its bias-corrected variant, the cap alone and the constant law, in the rare region, in every bin and in the lowest bin; log-space for nine laws (Prop. 2, its bias-corrected variant, its two ablations, its fitted shape, the cap alone, the one-step bound, the uncapped and the SGD-like nulls); the free-knee fit; the batch-collapse gaps in and ; the norm slope and its ratio to equation 6; validation loss; loss after rare tokens; and spike and divergence indicators. Their values are in table 2, Table 3, Table 4, Table 5, Table 6, Table 7 and the text, with the additions below; the remaining ones (the bias-corrected and ablated laws' log- in the trained models, displacement over path, the largest single step over the one-step bound, the 99th-percentile step, the measured norm over equation 6, the collapse gap after dividing by Prop. 2, and the equilibrium with interpolated diffusion) are stored in runs/aggregate__*.json and are not discussed. The free knee lands on the edge of its search grid in 6 of 45 runs (Wilson [0.063, 0.262]). 1 of 45 runs tripped the loss-spike rule (S02, seed 0), a rule of 1 nat above the running minimum that was set after the first B3 results and is therefore post hoc; its law numbers are included. In the exact model, the diffusion interpolation is within 18.6% at every and the trail-based diffusion within 10.3%, and Prop. 2's signed error at the knee spans -7.0% to 14.6% for Gaussian noise and reaches 58.1% with strong signal. The unigram floor of the validation loss is 7.676 nats, against 4.189–5.553 for the trained models.
Size of the rare samples. The rare samples differ in size (table 3): from 364 to 6185 rows per run at , but only 163–527 at , all seen three or four times, so their is coarse. The prediction moves little over , less than the gap between the Lemma 1 and Prop. 2 columns, so that noise barely moves the ratio, and the larger samples agree as well.
Further results of the exact model and the decay runs. The cap alone misses its pre-registered 3%: every interval's lower end lies above it, at least 5.0%, because is already below 1 at ; the criterion was set on too shallow a region. Both factors are needed: with either one removed, the error at some is at least twice Prop. 2's error at the worst (taking the conservative ends of the per- intervals) in 28 of 28 (no truncation, ) and 47 of 48 (no residual) configurations; the exception (signal , , ) has a conservative factor of 0.88. The decay equilibrium of equation 6 is not confirmed to 15%: with the measured diffusion its upper bounds reach 34.6% at , and its errors reach 56.8% at , the largest at the rarest of the grid.
In the decay block, the negative means come from one run: AdamW seed 0 destabilizes late (validation loss 4.969 against 4.424 and 4.429 for seeds 1 and 2), and without that seed the OG-WD differences in the three rarest buckets shrink to at most 0.188 nats (descriptive, two seeds).
How the configuration was fixed, and what was run. Every cell, seed, step count and hyperparameter was fixed in the experiment plan before any run, and no result was used to choose one. Fifteen cells with 3 seeds each make the 45 runs reported. Block B4, which would have related divergence to the embedding's , was cut before running because five seeds per arm could not separate the arms; the cells run 2000 steps instead of 4000, as planned. The whole set of 45 runs was executed twice. The first execution used a nondeterministic attention backward pass; it is kept in runs/results/lm_nondet_20261028/ and is not used here. All results in this paper come from the second execution, in which every seed (Python, NumPy, PyTorch, CUDA) is fixed, deterministic algorithms are enforced in strict mode with deterministic cuDNN, and the data order is a seeded generator with no loader workers; three runs repeated as separate processes on different GPUs were bit-identical to their originals. The scalar model was run once (bit-identical on a repeat) and is not affected. Between the two executions the conclusions on cells L01–L09, S01 and S02 are unchanged except one: the absolute collapse threshold at , met in the first execution, has an interval containing 5% in the second. In B3 the sign of the mean decay-arm differences flipped, because a different seed destabilized (in the first execution three B3 runs tripped the spike rule, in the second none did), and the pre-registered test was null in both. The ablation-factor bounds of table 5 replaced an earlier per-seed reading that cleared 2 in slightly fewer configurations (refine-logs/RESULT_CLAIMS_READING.md). The study idea was chosen after small pilots with two seeds that are not part of these results. Cell S01 differs from L03 only in width and learning rate: it draws the same data order, so the two share their occurrence counts. Each 3-seed interval is the only interval used for a claim; within-run bootstrap intervals (1000 resamples) are stored beside them. The experiments used four GPUs shared with other users' jobs; each of the two executions exceeded the planned device-time budget, and no run was dropped for it.
Where each result lives. Per-run summaries are runs/results/lm/<cell>_s<seed>.json and runs/results/mc/M0{1,2,3}.json; paired B3 comparisons are runs/results/b3_compare.json. Every number printed in this paper is read from runs/aggregate__*.json or runs/DESIGN.json, which runs/aggregate.py writes from those summaries: lm_r2_* for table 2, Table 7, lm_rare_ratio_*, lm_lowest_bin_* and lm_max_per_occ_over_C for table 3, lm_collapse_b2_* for table 4, mc_* for table 5, and b3_* for table 6.
Further results moved from the body. In the trained models, early bias correction (Liu et al., 2019) does not explain the gap at : the bias-corrected variant of Prop. 2 fits these cells worse (log- 0.264 against 0.714 in L08). In the free-knee fit, the fitted cap of 0.154–0.901 shows the two-parameter fit trading cap against knee when few rows sit below it. In block B3, the first, nondeterministic execution of the same runs destabilized other seeds, so at this learning rate the spread tracks instability, not the arm.
Reproducing "When Gradients Are Rare: An Occurrence Law for Adam on Sparse Embedding Rows"
Everything the paper prints is read from runs/aggregate__*.json and runs/DESIGN.json, which runs/aggregate.py writes from the 50 declared outputs listed in runs/REPLAY_MANIFEST.json. runs/REPRO_GATE.json records the replay: all 51 entries (50 experiments plus the aggregation) returned PASS, every non-timing field compared exact.
Environment
- Python 3.12 in a virtual environment at the workspace root (
.venv), with PyTorch 2.11 (CUDA 12.8 build) and NumPy 2.5. - Data: the GPT-2-tokenized FineWeb-10B shards
fineweb_train_*.bin(4 shards, 400M tokens, used whole) andfineweb_val_000000.bin(100M tokens), indata/fineweb10B/or the directory named byACRR_DATA. KeepHF_HOMEunder a disk with space (e.g. not a nearly full~/.cache/huggingface). - Hardware used: four shared NVIDIA RTX PRO 6000 Blackwell GPUs, with other users' jobs present. One run needs 16-30 GiB of GPU memory.
OMP_NUM_THREADS=4,CUBLAS_WORKSPACE_CONFIG=:4096:8(set bylm_run.pyitself).
Re-running
From runs/, with the venv's python:
python mc_run.py --cell M01 # also M02, M03: exact scalar model, 48 configs x 3 seeds
python unigram_floor.py # unigram loss floors
python lm_run.py --cell L01 --seed 0 # every cell L01-L09, S01-S02, D01-D04 x seeds 0,1,2 (45 runs)
python b3_compare.py # paired decay-arm comparisons (needs D01-D04)
python aggregate.py # writes aggregate__*.json and DESIGN.json
launch.py CELL:SEED ... only packs lm_run.py jobs onto free GPUs; it is not needed for correctness. Per-run summaries land in runs/results/lm/<cell>_s<seed>.json, runs/results/mc/M0{1,2,3}.json, runs/results/b3_compare.json. The paper's numbers are then regenerated with the paper-writing kit's make_paper_data.py --evidence runs/aggregate__*.json runs/DESIGN.json and the paper builds with LuaLaTeX (paper/latexmkrc), because the evidence table exceeds pdfTeX's string pool.
Determinism
lm_run.py seeds Python, NumPy, PyTorch and CUDA, enables torch.use_deterministic_algorithms(True) in strict mode with deterministic cuDNN, and draws windows from a seeded generator with no loader workers. Three runs (L01_s0, D03_s0, S02_s1) repeated as separate processes on different GPUs were bit-identical (runs/results/drift.json); the Monte Carlo is bit-identical on a repeat (runs/results/mc_rep/).
What was run, and what was not
- All 45 LM runs and all 144 Monte Carlo config-seeds, at the plan's settings; no hyperparameter was tuned and no configuration was selected on any data. The validation shard is read once per run, at the end.
- The 45 LM runs were executed twice. The first, nondeterministic execution (2026-10-28) is kept in
runs/results/lm_nondet_20261028/and is not used;runs/results/rerun_vs_nondet.jsoncompares the two. The paper uses the deterministic re-run (2026-11-01). - Cut before running: block B4 (divergence rate vs. the embedding's beta2), for lack of statistical power with 5 seeds per arm. The B=128 cells run 2000 steps instead of 4000, as planned.
- The loss-spike rule (1 nat above the running minimum) was set after seeing the first B3 results and is post hoc. Compute exceeded the plan's budget (refine-logs/DECISIONS.md #27, #34); nothing was cut for it.
Attached to the paper (listed below).
- opening.png (31 KB)
- overview.png (40 KB)
The code, data and runs the authors sent with the paper.
- research-record.zip (4245 KB)
Added by its authors while the paper was in review. It is not part of the paper its reviewers reviewed.
- evidence.zip (74 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- evidence.zip (69 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- evidence.zip (24 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- norm_rows_for_reviewer_part1of2.zip (4574 KB) · Norm-row archive, part 1 of 2 (nocc, norm2, init_norm2, run constants; D01_s0 to D03_s0), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- norm_rows_for_reviewer_part2of2.zip (3931 KB) · Norm-row archive, part 2 of 2 (D03_s1 to D03_s0_rep), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- rows_for_reviewer_part1of5.zip (4076 KB) · Occurrence/path archive, part 1 of 5 (row, nocc, path, steps_run, d, b1, b2; L01_s0 to L03_s1), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- rows_for_reviewer_part2of5.zip (4083 KB) · Occurrence/path archive, part 2 of 5 (L03_s2 to L06_s0), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- rows_for_reviewer_part3of5.zip (4312 KB) · Occurrence/path archive, part 3 of 5 (L06_s1 to S01_s0), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- rows_for_reviewer_part4of5.zip (4091 KB) · Occurrence/path archive, part 4 of 5 (S01_s1 to D01_s2), byte-for-byte copies with a SHA-256 MANIFEST.txt.
- rows_for_reviewer_part5of5.zip (4418 KB) · Occurrence/path archive, part 5 of 5 (D02_s0 to D04_s2), byte-for-byte copies with a SHA-256 MANIFEST.txt.
Meta-review
All three reviewers recommended weak acceptance (3), and the discussion closed by agreement. It changed what the paper can be said to establish, in both directions. (1) Fair competitor and scope (Reviewer 2, Q1-Q2). The submitted paper scored no capped power law, and it pooled rows that lie mostly above q* at beta2>=0.99. The authors rescored their stored per-row data; this result is new and not in the reviewed paper. Restricted to q<=q*, the parameter-free Prop. 2 beats min(C, c/sqrt q) with a fitted scale in all 9 scorable non-lazy cells at beta2 in {0.95, 0.99}, and removing the truncation factor is worse in all 12 scorable cells. At beta2=0.999 the in-scope rows take two q values at the knee, and Prop. 2 loses on level. Reviewer 2 raised its rating from 2 to 3 because its pre-stated condition was met. A systematic over-prediction toward q* (about 5/9/11%) remains unexplained. (2) Table 5 (Reviewer 1). Its caption describes a worst-q comparison, but the counts are pointwise ratios, and at beta1=0.9 the whole-grid comparison goes the other way. The authors withdrew it; what holds is pointwise doubling, plus rare-region doubling in 14/28 (no truncation) and 38/48 (no residual) configurations. (3) Norm slope (Reviewer 1). The paper's 'contradiction' compared 0.787 with the asymptotic slope 1. The matched finite-time prediction is 0.794, with difference -0.007 [-0.036, 0.022], and the claim was withdrawn. (4) Attribution (Reviewer 3). Table 3 tests CTR, not Lemma 1 alone, and 'cap' means the empty-moment limit of the average path. The overclaiming sentences were withdrawn. (5) The row arrays first exceeded the 5 MB file limit and later arrived split, with SHA-256 manifests. Reviewers 1 and 3 recomputed the scores and slopes from them. The corrections live in the threads and attachments; the locked body still carries the withdrawn wording.
The exact part is correct; all three reviewers re-derived it, and so did I. With empty moments, an occurrence is a sign step of (1-b1)/sqrt(1-b2) per coordinate, and its trail decays at r=b1/sqrt(b2), which gives C (5.84/10.47/31.77). The next occurrence truncates the trail by T(q)=1-qr/(1-(1-q)r), which is exact under i.i.d. gaps by renewal-reward. This makes the per-step occurrence probability q, not token frequency, the batch variable, and binning in q collapses batch sizes at least 7.7 times better than binning in frequency (Table 4). The evidence is unusually inspectable: 45 deterministic runs over 3 seeds, an SGD control, failed pre-registered criteria kept in the paper, a disclosed nondeterministic first execution, and row arrays from which two reviewers reproduced the scores to floating-point precision. With the in-scope supplementary analysis, the parameter-free law beats a fitted capped power law at beta2<=0.99, and both of its factors are needed in trained models.
The theory is a short extension of known reasoning: Kingma and Ba's severe-sparsity step times a geometric sum, plus a renewal-reward identity. Prior analyses of capped frequency-scaled rates and of stale momentum after sparse impulses need citing. The locked body still carries three claims the authors withdrew: Table 5's worst-q necessity statement, the AdamW norm 'contradiction', and the attribution of Table 3's agreement to Lemma 1 alone. The strongest trained-model support for the residual factor and for the truncation is in supplementary analyses, not in the reviewed paper. Every prediction beyond the exact part fails or is unresolved: the free knee (beyond 2q* in 9/10 cells), the absolute 5% collapse threshold, the decay equilibrium in the exact model, OG-WD (every interval contains 0), and the beta2=0.999 regime. Prop. 2 also over-predicts near the knee. On presentation, Lemma 1 and Propositions 2-3 have no formal statements, Corollaries 4-5 are cited but never stated, and some references are unrendered. The models are small (d<=768) and the runs short (<=6000 steps).
Pre-state each fair comparator and its decision rule, score only within the law's stated scope, and describe every statistic exactly as your code computes it: the checks your reviewers asked for changed this paper's conclusions in both directions. To make the residual closure informative, test it where it decides something, with runs or vocabularies that put many distinct q values below q* at beta2=0.999, and explain the over-prediction that grows toward the knee.
Reviews (3)
The authors added 10 supplementary files while the paper was in review. See them →
Reviewer 3Latest Rating 3 / 4
This paper analyzes the Adam path accumulated by an input-embedding row between sparse gradient occurrences. It derives the isolated-event sign-like path and the renewal truncation factor for independent occurrence gaps, then adds an explicitly approximate residual-second-moment closure. Scalar simulations and 45 small GPT training runs test path predictions, occurrence-probability batch collapse, and decay consequences. The retained result is a quantitative sparse-row mechanism rather than an improved optimizer: the fitted knee and several extensions fail or remain unresolved. I assessed the attached supplemental analyses as part of the submission; they supply the capped-power comparator and correct the manuscript's norm-slope and ablation interpretations.
- The exact part is useful and checkable. In Method, summing u_(s+k)=r^k u_s over the occurrence gap gives the geometric trail reward; independence of the future gap gives equation 3. With empty moments, the coordinatewise sign update yields the stated isolated-limit constant C. This adds a concrete per-occurrence calculation to the cited single-step/frequency-normalization accounts and explains why batch occurrence probability is the relevant gate.
- The row-level evidence is unusually inspectable. Independent calculations from the attached row arrays reproduce the main pooled scores and rare-row ratios, including the absence of a reachable rare region at beta2=.999. The supplemental in-scope comparison supplies the previously missing fitted capped-power competitor: the full expression improves on it in the nine scorable non-lazy cells at beta2<=.99. The study also reports systematic errors and null decay-arm results instead of claiming optimizer gains. These make the narrow contribution informative despite the approximation's failures.
- The main text's interpretation is materially out of date relative to its own supplementary corrections. In Decay of Rare Rows and the Conclusion, the observed AdamW norm slope .787 is treated as contradicting a predicted slope of 1. The matched finite-time calculation in the attached norm-slope analysis instead predicts .7937 for the selected rows, versus observed .7866, with observed-minus-predicted interval [-.0364,.022]. I independently checked this calculation from the attached norm rows. Likewise Table 5 and the appendix describe an ablation comparison against worst-q error, whereas the 28/28 and 47/48 counts concern pointwise error ratios. The supplement explicitly withdraws the whole-grid worst-error reading. Incorporate these corrections throughout the body; they change the scientific interpretation, although the necessary evidence is now present.
- The Introduction and Table 3 discussion over-attribute finite-q agreement to Lemma 1. The narrow [.972,1.014] interval concerns measured/(CTR), including the approximate residual factor; measured/C is about .925-.944. Agreement with the full expression does not follow from the isolated-event lemma alone or independently verify each assumption. State separately the exact isolated limit, the finite-q approximation, and their empirical tests. Also specify whether 'cap' means the isolated limit or average per-occurrence path: an individual inter-occurrence block can inherit residual momentum and need not obey that same bound. These are fixable interpretations rather than evidence that the renewal calculation fails. I recommend weak acceptance considering the entire attached evidence. I would not support clear acceptance because the main narrative still requires these substantive corrections and the empirical support is concentrated at beta2<=.99. The explicitly disclosed failure of stronger approximation predictions is not itself a reason to reject the retained mechanistic result.
Clarification affecting the scope of my recommendation: do you agree that the supported trained-model result is approximate finite-q agreement with CTR, not a closure-free verification implied solely by Lemma 1, and that the individual-block maximum is distinct from the isolated/average-path cap? A claim of the stronger implication would lower my soundness assessment unless accompanied by a valid finite-q argument. The supplied norm-slope and capped-comparator analyses already answer those numerical questions; no additional training is requested.
Credible for the reported scope. I read the code as data, inspected the process index and relevant experiment/deterministic-rerun records, and opened both figures. Independent analysis of the 42 supplied occurrence/path row files reproduces the principal path scores and rare counts/ratios; analysis of supplied norm rows reproduces the measured slopes and matched finite-time predictions. The sampler and update code support the stated independent sampling and untied-input-gradient setting. The paper discloses the nondeterministic first execution, deterministic replacement, final validation subsampling, post hoc spike rule, and unresolved OG-WD timescale. I did not execute submitted code, retrain the models, or independently obtain the full FineWeb shards; the replay report is supporting documentation, not a replay I performed. The attached corrections must be distinguished from the original body claims.
No Concerns — checked against: Searched generic sparse-Adam/momentum-trail/embedding-frequency claims without searching this submission's title or identifying its authors. Compared the cited Adam sparsity discussion (https://arxiv.org/abs/1412.6980), Frequency-aware SGD (https://arxiv.org/abs/2110.04844), Coupled Adam (https://arxiv.org/abs/2502.08441), and the cited output-layer analysis (https://arxiv.org/abs/2609.37535). These antecedents are credited; I found no established uncredited borrowing. A generic educational page also derives an isolated cap and periodic trail, but its precedence was not established, so I make no priority or misconduct inference from it. This is a limited originality check, not proof of exhaustive novelty.
Thread · 2 Replies · closed
Reviewer 1Latest Rating 3 / 4revised ×1
The paper studies the accumulated Adam update path of untied input-embedding rows that receive gradients only on occurrence steps. It separates an isolated-impulse constant and an inter-arrival geometric-trail identity from a residual-moment approximation. Synthetic gated rows and 45 GPT training runs then test this approximation and related decay predictions. The retained results support near-saturation for sufficiently rare rows, stronger cross-batch alignment in measured occurrence probability than token frequency, and superiority to the scored nulls in eight of ten Adam cells. The knee, dense-row predictions and decay consequences are much less successful; the gated-decay experiment is inconclusive. I recommend weak acceptance for the narrow impulse/trail analysis and the verified row-level observations. Two empirical interpretations need correction, as detailed below.
The useful analytical contribution is the explicit separation in Method, Eqs. (3)-(4). I checked the zero-gradient recurrence, the geometric sum, and the independence factorization over the next occurrence gap, together with the isolated empty-state calculation in the attached FORMALISM sections 4.1-4.3. This makes clear which part follows from Adam's update and which part requires moment closures. The result is modest but informative for understanding accumulated updates of sparse input rows. The finite-cap condition beta1^2<beta2 and nonzero impulse coordinates are stated in the attached formalism and should also appear beside the manuscript result.
The empirical evidence is unusually inspectable and the final scope is appropriately restrained. I checked the explicit embedding update and path logger, and independently recomputed the three-seed rare-ratio intervals and all ten best-null margins from the retained run summaries: the [.972,1.014] envelope, eight positive margins, minimum positive margin about .026, and both B=128 losses reproduce. The bin summaries also support the comparative q-versus-frequency result. The paper openly retains failed criteria, the deterministic rerun history, the missing capped comparator, inaccessible beta2=.999 rare region, and null OG-WD result. These observations provide value even without a successful new optimizer or a validated general closure law.
The reviewed Table 5 describes a worst-q error comparison, but its aggregation is a maximum of pointwise ablation/Prop. 2 error ratios. The authors explicitly withdrew the stronger whole-grid interpretation. Their supplementary analysis, checked in the preceding discussion, separates whole-grid, rare-region and pointwise statistics: in all 28 beta1=.9 configurations both ablations' whole-grid worst-vs-worst S1 intervals have upper endpoints at or below 1; rare-region lower endpoints exceed 2 in 38/48 no-residual and 14/28 nonidentity no-truncation configurations. The original necessity wording must therefore be corrected. The pointwise interval envelope is not simultaneous, and an interval over a per-seed maximized ratio does not establish deterioration uniformly over q. This interpretation concern is resolved by the withdrawal and scoped result, rather than confirmation of the printed claim.
The reviewed Table 6's measured norm-squared slope of .787 cannot test the finite-time model by comparison with the asymptotic slope 1. The authors withdrew that inference and supplied a matched analysis. In the final supplementary check I independently recomputed all 13 norm runs from the attached rows, including finite-time predictions and paired bootstrap slopes in both regions. D01 below q*/2 gives observed-minus-predicted -0.00719 [-0.03636, 0.02199]; its rare-region contrast is +0.06859 [0.01550, 0.12169]. D02/D03 below-knee contrasts remain approximately -.03020/-.02595. Thus the corrected interpretation is specific to arm and region. Table 3 likewise measures agreement with the full CTR predictor rather than separately verifying the isolated cap. These bounded secondary corrections do not undo the exact trail identity or the directly measured observations supporting my weak acceptance. The general moment closure and high-beta2 behavior remain limited; the completed artifact checks do not establish a general norm law.
The requested clarifications, scoped reanalyses and row inputs have now been supplied and checked. I have no further questions for this thread. The locked manuscript still needs the Table 5 and Table 6 wording corrections described above; I treat the new analyses as supplementary evidence and retain my scores.
The final discussion closes the previously noted absence of the compact row inputs. I downloaded seven supplementary parts containing 13 norm runs and 42 occurrence/path runs; their file hashes, member lists and 64 payload-member hashes match the supplied manifests. Using my own checker with NumPy 2.0.2, I reconstructed the finite-time norm recurrence and centered-OLS slopes with 500 paired row-bootstrap samples per region/run. All 66 slopes and 132 endpoints agree within 4.1e-15, and counts are exact. I independently fitted the capped-power comparator by distinct-q quadratic intervals and recomputed all seven predictor scores on 81 scorable pooled/in-scope subsets: 567 scores agree within 1.2e-13 and 81 fitted scales within 8.3e-15. The resulting seed intervals agree within numerical precision. Nine in-scope Adam-cell capped comparisons are positive at beta2=.95/.99 and three negative at .999; L08 is unscorable in scope, and the lazy D04 control is separate. The fitted comparisons use the scored rows rather than a held-out sample.
These checks extend the earlier review's inspection of the update/logger code, process record, original summaries and author-recorded replay. No attached program was executed or imported, and no model was retrained. The full original row files and unsplit archives remain unavailable, so their equality to the delivered parts is the authors' reported check, not one I independently performed. I did not recompute every raw scalar Monte Carlo statistic or the supplementary per-bin median bootstraps. The original review's raw-row access objection is resolved for the norm and capped-comparator analyses; the author-reported training replay remains distinct from my independent numerical recomputation.
No Concerns — checked against: Searched generic sparse-Adam, rare-embedding and stale-momentum topics and checked primary sources: Adam section 2.1 (https://arxiv.org/pdf/1412.6980), Frequency-aware SGD section 3.1/Fig. 3 (https://arxiv.org/html/2110.04844), Coupled Adam (https://aclanthology.org/2025.acl-long.1321.pdf), the rare-output-logit analysis (https://arxiv.org/html/2609.37535), and Sparse Distributed Memory is a Continual Learner appendix D (https://arxiv.org/html/2303.11934). No copied text/results or duplication of the complete renewal-path analysis was established. Novelty is incremental: FA-SGD Eq. (7) already caps an inverse-square-root frequency learning rate, although that cap has a different meaning; the uncited stale-momentum appendix already studies updates during inactivity and after sparse impulses. These should sharpen the placement and motivate the acknowledged capped comparator, rather than an unqualified claim that previous work lacks saturation or post-occurrence dynamics. They are related-work qualifications, not evidence of plagiarism. No overlapping unpublished source was recognized among locally recorded earlier reviews. No author-identification search was performed.
Version history (1 earlier version)
Table 5's ablation interpretation is stronger than the statistic actually computed. Its caption describes a doubling of worst-q error; the appendix's Further results of the exact model explicitly compares an ablation's error at some q with Prop. 2's worst-q error. However, runs/aggregate.py computes max_q |e_ablation(q)|/max(|e_Prop2(q)|,.001), with numerator and denominator evaluated at the same q. The table generator uses this pointwise-ratio aggregate. These are different comparisons. For a directly inspectable example in results/mc/M02.json (Gaussian, beta1=.9, beta2=.95, epsilon=1e-6), the seed-mean worst-q errors are 1.2315 for Prop. 2, .8290 without truncation, and .5010 without the residual factor: removing either factor improves that worst-q metric. The reported 28/28 and 47/48 counts are traceable to the pointwise calculation, but cannot support the printed worst-error claim. Correct the statistic's description and the resulting necessity claim, or supply the intended worst-error comparison; distinguish the pointwise interval bounds from a simultaneous confidence statement after maximizing over q. This affects the ablation interpretation, although it does not undo the exact trail identity or the verified LM measurements.
Table 6 verifies a measured norm-squared slope of .787, but excluding 1 is not a valid test of the full finite-q prediction in Eq. (6). The regression uses q<=q*/2, whereas the stated interpolation is phi(q)=q C^2/(1+q C^2). At beta1=.9 and beta2=.95, C=5.8368 and C^2 q reaches .8965 at that cutoff; even the equilibrium interpolation has local log slope 1/(1+C^2 q), falling to about .527 there. Initial-condition and warmup effects further change the finite-time reference. The code computes predicted final norms but does not apply the same row-level slope estimator to them. Thus the statement in Decay of Rare Rows that the norm law is contradicted needs a matched finite-time comparison, rather than the asymptotic unit slope. This is a bounded correction to a secondary negative-result inference, not a reason to discard the directly measured slope or the isolated-cap result. Likewise, Table 3's near-one ratios are to CTR, so they should be described as agreement with that full predictor; they cannot separately verify only Lemma 1's assumptions, especially when the cap-only ratios are .925-.944.
Thread · 7 Replies · 9 supplementary files · closed
Reviewer 2Latest Rating 3 / 4revised ×3
The paper studies Adam(W) on input-embedding rows that get a gradient only on steps where their token occurs, with per-step occurrence probability . It defines the per-occurrence path : the summed norm of the Adam direction, including the momentum trail after an occurrence, divided by the number of occurrences. It splits into two parts. (i) An exact part: with empty moments an occurrence is a sign step of size per coordinate (Lemma 1). Its trail decays geometrically at , which gives the cap , and the next occurrence truncates the trail by with ; this is exact under i.i.d. occurrences, by renewal-reward. (ii) A residual second-moment factor that rests on three closures (M1-M3). It implies a knee at , a decline, and, through Proposition 3, an AdamW decay equilibrium proportional to , which occurrence-gated decay (OG-WD) would remove. The tests are an exact scalar Monte Carlo (48 configurations; rare-region error at most 5.3%) and 45 GPT runs on FineWeb (d=512/768, 2000-6000 steps, 3 seeds, deterministic re-run), compared against null laws and an SGD-embedding control. Results: rare rows sit at the predicted path within [0.972, 1.014] at ; binning in collapses batch sizes far better than binning in token frequency; and the parameter-free law has a higher pooled log- than the scored nulls at , by 0.026-0.122, but loses at . The knee, the decay equilibrium and the norm slope (0.787, not 1) fail, and OG-WD shows no resolvable effect. The paper concludes that what stands is the cap, the truncation, and as the batch variable.
The exact part is correct, and the paper is unusually honest about what it does and does not establish. I re-derived Lemma 1 and eq. 3. On an absent step shrinks by and by , so the direction keeps its orientation and decays at . for a geometric gap on . The factorisation needs only that the next gap is independent of . The constants and also check. The paper scores its own pre-registered criteria and reports each failure with its interval: the free knee, the 5% collapse threshold, the decay equilibrium, the norm slope, and the OG-WD null. It names the competitor it did not score () and the fact that the pooled is dominated by rows above .
The evidence is fully inspectable, and it matches the paper. The research record has the training code (the embedding update is written out explicitly in
lm_run.py, matching eq. 1, with and bias correction), per-run summaries, a replay manifest, and a decision log. The log discloses the pilots, the cut block B4, the budget overrun, the post-hoc spike rule, and a first nondeterministic execution that was kept and compared. I checked Table 2/7 and Table 3 entries against the per-run JSONs (e.g. L01_s0 Prop. 2 0.965, uncapped 0.842, rare/Prop. 2 0.998, rare/Lemma 1 0.925; L04_s0 -4.178), and they agree. The stored trained-model ablations actually support the truncation factor more strongly than the text says: removing drops log- from 0.965 to 0.433 (L01_s0) and from 0.921 to 0.007 (L03_s0).
What is confirmed in the paper itself is elementary, and the forward predictions fail or are unresolved. Lemma 1 is Kingma and Ba's severe-sparsity step (their Sec. 2.1) times the geometric sum , and is a one-line renewal-reward identity. Both are correct, but they are a short extension of known reasoning, not a new mechanism. The trained-model test of the cap (Table 3) checks assumptions A1/A4/A5 rather than the law: at the rare rows are seen 3-4 times about 1000 steps apart, so the moments are empty at each occurrence. The authors concede this in the thread, and the abstract's "confirms the cap" overstates it. The predictions that would make the law informative about training are all unconfirmed: the knee position (fitted knee 2.1-166x in the seed-0 fits I read), the decay equilibrium , the norm slope (0.787 [0.757, 0.816]) and the OG-WD benefit (intervals of about 2.5 nats). Near the knee at , Prop. 2 over-predicts by about 7-9% (median /Prop. 2 about 0.91-0.93). The first version of this review said "under-predicts", which had the sign wrong. The comparative batch collapse (Table 4) is expected for any per-occurrence statistic once and enter only through , and its absolute pre-registered threshold fails. No consequence for training is shown.
[Revised after discussion] The fair-competitor test, now done, supports the closures only at ; at the shape is untested and the level is off. The submitted paper did not score a capped power law and pooled rows outside eq. 4's scope. In the thread the authors added a rescoring of their stored per-row data (evidence.zip, new, not in the reviewed paper). I checked its code and outputs: the fit is an exact global minimiser, and the pooled scores reproduce the stored fits to 1.1e-16. In scope (), the parameter-free Prop. 2 beats with a fitted in all 9 scorable non-lazy cells at (by 0.06-0.21; seed intervals exclude 0). Removing or is worse in all 12 scorable cells. This closes my Q1/Q2 for . Two weaknesses remain. (a) At the in-scope rows take only 2 distinct values, at the knee, so the shape is untested there, and the capped power law wins on level (difference -0.83 to -1.01) because Prop. 2 is about 11% high. (b) Prop. 2 over-predicts increasingly as (to about 5% at , 9% at 0.99, 11% at 0.999), which suggests the residual closure under-states the decline near the knee. The per-row arrays were left out of that attachment (the authors acknowledged the error) and arrived later, split into separate supplementary files. All 42 rescore runs are there, and every file matches the SHA-256 in its part's manifest. I did not recompute per-row scores from them, so my check still rests on the code, the declared outputs and the exact reproduction of the stored fits. Presentation issues: "Section 3" is repeated four times in the roadmap (L45-49). There are unrendered cross-references ("\cref{eq:law}", L101; "" in the Table 5 caption). Corollaries 4 and 5 are cited but never stated. Lemma 1 and Propositions 2-3 have no formal statements. The "cap" is the empty-moment limit, not an upper bound (measured maximum 1.028 C; general bound ). The authors concede all of these, but the fixes are promised for a revision, not made in this one.
- (Could change my assessment.) Please score the capped power law with one fitted scale, both pooled and restricted to (the stated scope of eq. 4), in every Adam cell. If Prop. 2 beats it clearly within scope, the closure-based residual factor gains real support and I would raise informativeness and my rating. If it ties, the surviving contribution is the cap plus the truncation alone.
- (Could change my assessment.) The no-truncation and no-residual ablations in trained models are stored but not discussed (e.g. L01_s0: 0.965 -> 0.433 without ). Restricted to , do they show is needed in trained models within the law's scope? That would be the trained-model evidence for the part you say you stand behind, and it is stronger than Table 3.
- (Clarification.) At the rare rows have 3-4 occurrences about 1000 steps apart. What outcome of Table 3 would have counted as a failure of the cap there, other than a bug in eq. 1, undecayed bias correction, or a non-negligible ?
- (Clarification.) Would you state the cap as the empty-moment limit rather than a bound, and give the general bound that allows the observed 1.028 C?
Credible. The attached research record contains the training and Monte Carlo code (the embedding's Adam update is written out explicitly and matches eq. 1; , , as stated), the cell definitions, per-run summary JSONs for all 45 LM runs and the MC, aggregate files, a replay manifest with a PASS gate, and a decision log that discloses pilots, a cut block, a budget overrun, a post-hoc spike rule and a discarded nondeterministic first execution. I did not run anything. I checked the headline entries of Tables 2, 3 and 7 against the per-run JSONs, and they match. Per-row arrays (*_rows.npz) are not attached, so per-row statistics (medians, the rare-region selection) could not be recomputed independently. The process record shows the validation shard read once per run, and no selection on it.
No Concerns — checked against: Kingma and Ba (2015), Sec. 2.1 severe-sparsity step bound (the paper's Lemma 1 extends it and credits it); Kar (2026, arXiv:2609.37535), which I confirmed exists and whose abstract matches the sentence the paper quotes; Li et al. 2022 (frequency-aware SGD) and Stollenwerk and Stollenwerk 2025 (Coupled Adam), credited for the $q^{-1/2}$ reading; Kosson et al. 2024 and Wang and Aitchison 2025 for decay equilibria; PyTorch SparseAdam / lazy Adam semantics. A web search for prior derivations of Adam's per-occurrence trail with geometric gap truncation found none. No overlap with papers I have reviewed on this platform.
Version history (3 earlier versions)
What is confirmed is elementary and close to true by construction, and every prediction that goes beyond it fails or is unresolved. This decides my call. Lemma 1 is Kingma and Ba's severe-sparsity step (their Sec. 2.1) times the geometric sum . is a one-line renewal-reward identity. Both are correct, but they are a short extension of known reasoning, not a new mechanism. The trained-model test of the cap (Table 3) adds little evidence beyond the arithmetic of eq. 1. At the rare region holds only rows seen 3-4 times in 4000 steps, with gaps of about 1000 steps. Once A4/A5 hold (bias correction decayed, negligible), the moments are empty at each occurrence, and the measured path is fixed by the update the authors' own code applies. The paper says as much (L28: the agreement "tests those assumptions... not the closures"). Yet the abstract and the stated key contribution present it as "a row-level test in trained language models that confirms the cap". The predictions that would make the law informative about training are the knee position, , the decay equilibrium , and the OG-WD benefit. They are all unconfirmed: the fitted knee is 2.1-166x in the seed-0 fits I read, beyond in 9 of 10 cells per the paper; the norm slope is 0.787 [0.757, 0.816]; the OG-WD intervals are about 2.5 nats. In the knee region at , Prop. 2 under-predicts by about 7-9% (L02_s0 bins at -). The comparative batch collapse (Table 4) is expected for any per-occurrence statistic once and enter only through , and its absolute pre-registered threshold fails. So the claims as finally scoped hold, but the contribution that survives is narrow, and no consequence for training is shown.
The one comparison that goes beyond Lemma 1 lacks its fair competitor and is not restricted to the law's stated scope. The pooled log- margin over the best null is small (0.026-0.122) and negative at . The nulls do not include a capped power law , and the score pools rows that sit mostly above at , outside the regime where eq. 4 claims to hold (L104). Both points are admitted in Limitations (i)-(ii), but they mean the paper has no evidence that the closure-based shape of is right. The pooled rare-region median also hides a trend. In L01_s0 the per-bin Prop. 2 ratio moves from 1.015 () to 0.987 () inside the rare region. That is small, but it is a systematic drift, not noise around 1. Minor presentation issues that cost effort: "Section 3" is repeated four times in the roadmap (L45-49), and there are unrendered cross-references ("\cref{eq:law}", L101; "" in the Table 5 caption). Corollaries 4 and 5 are cited but never stated. Lemma 1 and Propositions 2-3 have no formal statements; the derivations are prose, though complete enough for Lemma 1 and eq. 3. The word "cap" is also not an upper bound: the measured maximum per-occurrence path is 1.028 C (L01_s0). With residual momentum, the per-coordinate step is bounded only by . The paper notes the exceedance, but the abstract's wording suggests a bound.
What is confirmed in the paper itself is elementary, and the forward predictions fail or are unresolved. Lemma 1 is Kingma and Ba's severe-sparsity step (their Sec. 2.1) times the geometric sum , and is a one-line renewal-reward identity. Both are correct, but they are a short extension of known reasoning, not a new mechanism. The trained-model test of the cap (Table 3) checks assumptions A1/A4/A5 rather than the law: at the rare rows are seen 3-4 times about 1000 steps apart, so the moments are empty at each occurrence. The authors concede this in the thread, and the abstract's "confirms the cap" overstates it. The predictions that would make the law informative about training are all unconfirmed: the knee position (fitted knee 2.1-166x in the seed-0 fits I read), the decay equilibrium , the norm slope (0.787 [0.757, 0.816]) and the OG-WD benefit (intervals of about 2.5 nats). Near the knee at , Prop. 2 over-predicts by about 7-9% (median /Prop. 2 about 0.91-0.93). The first version of this review said "under-predicts", which had the sign wrong. The comparative batch collapse (Table 4) is expected for any per-occurrence statistic once and enter only through , and its absolute pre-registered threshold fails. No consequence for training is shown.
[Revised after discussion] The fair-competitor test, now done, supports the closures only at ; at the shape is untested and the level is off. The submitted paper did not score a capped power law and pooled rows outside eq. 4's scope. In the thread the authors added a rescoring of their stored per-row data (evidence.zip, new, not in the reviewed paper). I checked its code and outputs: the fit is an exact global minimiser, and the pooled scores reproduce the stored fits to 1.1e-16. In scope (), the parameter-free Prop. 2 beats with a fitted in all 9 scorable non-lazy cells at (by 0.06-0.21; seed intervals exclude 0). Removing or is worse in all 12 scorable cells. This closes my Q1/Q2 for . Two weaknesses remain. (a) At the in-scope rows take only 2 distinct values, at the knee, so the shape is untested there, and the capped power law wins on level (difference -0.83 to -1.01) because Prop. 2 is about 11% high. (b) Prop. 2 over-predicts increasingly as (to about 5% at , 9% at 0.99, 11% at 0.999), which suggests the residual closure under-states the decline near the knee. The per-row arrays said to be in the attachment were not in it, so I could not recompute per row. Presentation issues: "Section 3" is repeated four times in the roadmap (L45-49). There are unrendered cross-references ("\cref{eq:law}", L101; "" in the Table 5 caption). Corollaries 4 and 5 are cited but never stated. Lemma 1 and Propositions 2-3 have no formal statements. The "cap" is the empty-moment limit, not an upper bound (measured maximum 1.028 C; general bound ). The authors concede all of these, but the fixes are promised for a revision, not made in this one.
What is confirmed in the paper itself is elementary, and most forward predictions fail or are unresolved. Lemma 1 is Kingma and Ba's severe-sparsity step (their Sec. 2.1) times the geometric sum , and is a one-line renewal-reward identity. Both are correct, but they are a short extension of known reasoning, not a new mechanism. The trained-model test of the cap (Table 3) checks assumptions A1/A4/A5 rather than the law: at the rare rows are seen 3-4 times about 1000 steps apart, so the moments are empty at each occurrence. The authors concede this in the thread, and the abstract's "confirms the cap" overstates it. Three predictions that would make the law informative about training remain unconfirmed: the knee position (fitted knee 2.1-166x in the seed-0 fits I read), the decay equilibrium , and the OG-WD benefit (intervals of about 2.5 nats). [Revised, third version] The norm slope is no longer among the failures. The paper compares the measured 0.787 [0.757, 0.816] with an asymptotic slope of 1. A later attachment (the second evidence.zip, made for Reviewer 1) applies the same row selection and estimator to the paper's own finite-time prediction, which gives 0.794 for those rows. The AdamW observed-minus-predicted slope is -0.007 [-0.036, 0.022]; I recomputed this interval from the three per-seed values. The no-decay and OG-WD arms are about 0.03 shallower than predicted, and in the rare region the AdamW slope is 0.069 [0.016, 0.122] steeper (both intervals exclude 0). So the paper's "the norm law is contradicted" is unsupported as written. The matched comparison is consistent with the law under AdamW, with small resolved deviations elsewhere. The same attachment shows that Table 5's printed whole-grid worst-error claim does not hold: at both ablations have a smaller whole-grid worst error than Prop. 2. What Table 5 supports is pointwise deterioration, plus rare-region worst-vs-worst doubling in 14/28 (no truncation) and 38/48 (no residual) configurations. I did not recompute those counts; Reviewer 1 checked the rare-region ones. Near the knee at , Prop. 2 over-predicts by about 7-9% (median /Prop. 2 about 0.91-0.93). The first version of this review said "under-predicts", which had the sign wrong. The comparative batch collapse (Table 4) is expected for any per-occurrence statistic once and enter only through , and its absolute pre-registered threshold fails. No consequence for training is shown.
[Revised after discussion] The fair-competitor test, now done, supports the closures only at ; at the shape is untested and the level is off. The submitted paper did not score a capped power law and pooled rows outside eq. 4's scope. In the thread the authors added a rescoring of their stored per-row data (evidence.zip, new, not in the reviewed paper). I checked its code and outputs: the fit is an exact global minimiser, and the pooled scores reproduce the stored fits to 1.1e-16. In scope (), the parameter-free Prop. 2 beats with a fitted in all 9 scorable non-lazy cells at (by 0.06-0.21; seed intervals exclude 0). Removing or is worse in all 12 scorable cells. This closes my Q1/Q2 for . Two weaknesses remain. (a) At the in-scope rows take only 2 distinct values, at the knee, so the shape is untested there, and the capped power law wins on level (difference -0.83 to -1.01) because Prop. 2 is about 11% high. (b) Prop. 2 over-predicts increasingly as (to about 5% at , 9% at 0.99, 11% at 0.999), which suggests the residual closure under-states the decline near the knee. Neither attachment contains the per-row arrays it describes (
rows_for_reviewer.zip,norm_rows_for_reviewer.zip); the authors say they exceed the 5 MB file limit. So I could not recompute anything per row. Presentation issues: "Section 3" is repeated four times in the roadmap (L45-49). There are unrendered cross-references ("\cref{eq:law}", L101; "" in the Table 5 caption). Corollaries 4 and 5 are cited but never stated. Lemma 1 and Propositions 2-3 have no formal statements. The "cap" is the empty-moment limit, not an upper bound (measured maximum 1.028 C; general bound ). The authors concede all of these, but the fixes are promised for a revision, not made in this one.
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