Training-Memory, Storage, and Accuracy Trade-Offs of Magnitude-Selected Subspace and Multi-Locus Deletion Tuning

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Deletion tuning: how far can a model improve by removing weights? · Download Markdown · BibTeX

Abstract

Deletion tuning adapts frozen language models via binary masks $\mathbf{W}' = \mathbf{W} \odot \mathbf{M}$ ($\mathbf{M} \in \{0,1\}^{d_{\text{out}} \times d_{\text{in}}}$) on SwiGLU gate projections, yielding compact bitmaps (~4.4 MiB) but requiring 9.30 GiB of peak training memory on Llama-3.2-1B-Instruct—above continuous gate-only fine-tuning (7.03 GiB). We study how restricting learnable logits to static top-$p$ $|W|$ supports across single and multiple projections trades off training memory, wall-clock time, compressed-delta storage, and accuracy over 162 runs (3 seeds $\times$ 6 methods $\times$ 9 custom 75%/25% MMLU-Pro partitions, 1,946 fixed test questions), stratified into 3 development categories, 2 previously inspected off-target categories, and 4 uninspected confirmatory categories. Separating exact Wanda-prior membership from random negative-tail initialization shows 99.5% step-400 prior persistence (co-occurring with $\epsilon/\sqrt{\hat{v}_t} > 0.1$ on 99.7% of prior weights) and uniform ~0.89% deletion across all non-Wanda $|W|$ quantiles. Under the supplied mean-NLL rule in matched bfloat16, single-matrix gate restriction at $p=0.50$ and $p=0.20$ lowers peak memory to 6.80 and 4.17 GiB and masks to 2.54 and 1.35 MiB, changing 9-category accuracy by $-0.71$ pp (hierarchical seed+question 95% CI $[-1.59, +0.16]$; uninspected-4: $-0.18$ pp $[-1.68, +1.28]$) and $-2.40$ pp ($[-3.54, -1.30]$; uninspected-4: $-2.79$ pp $[-4.68, -1.03]$) relative to dense gate deletion (17.84%). Four-projection $p=0.20$ operating points ({gate, up, down, o_proj}, 8.16 GiB, 203 s, 2.15 MiB vs. 231.5 MiB zstd bfloat16 gate-tuning XOR deltas) recover $+2.36$ pp ($[+1.13, +3.64]$) over single-matrix $p=0.20$ ($+2.22$ pp $[+0.21, +4.28]$ on uninspected-4) to reach 17.80% (continuous gate: 17.83%; full fine-tuning: 18.16%). Results are scoped to 400-step 1B multiple-choice SFT.

1. Problem and Contribution

Deletion tuning adapts a pretrained language model by zeroing a learned binary subset of existing parameters while leaving every surviving weight value unchanged [1]:

$$ \mathbf{W}' = \mathbf{W} \odot \mathbf{M}, \qquad \mathbf{M} \in \{0,1\}^{d_{\text{out}} \times d_{\text{in}}}. $$

On Llama-3.2-1B-Instruct (268,435,456 weights across the 16 SwiGLU gate_proj matrices), learned binary masks compress to roughly 4.4 MiB (packbits + zstd)—over fifty times smaller than losslessly zstd-compressed bfloat16 weight-delta checkpoints from continuous gate-only or full-model fine-tuning [1, 2, 3]. Yet standard differentiable binary masking faces an acute training-memory and expressivity trade-off:

  1. Peak Training-Memory Overhead: Allocating one FP32 latent gate logit $g_{ij}$ plus two FP32 Adam moment buffers $(m_{ij}, v_{ij})$ per gate_proj weight consumes 9.30 GiB of peak GPU memory during 400-step supervised fine-tuning (SFT)—more than continuous gate-only fine-tuning (7.03 GiB) [2, 3]. Dense mask allocation rapidly becomes a bottleneck on larger backbones or multi-model distillation setups.
  2. Static Candidate Restriction vs. Multi-Projection Allocation: Lu et al. [1] noted conceptually that restricting learnable logits to a subset of candidate weights could save training memory and proposed combining masks by union. However, how preselecting a static top-$p$ weight-magnitude support trades off peak training memory, wall-clock runtime, compressed mask size, and held-out accuracy—and whether reallocating the saved gate budget across multiple Transformer projections recovers single-matrix capacity losses—has not been quantified under leak-free, exposure-stratified multi-seed controls.

We investigate these trade-offs on custom 75%/25% partitions of the released MMLU-Pro test collection [4] using Llama-3.2-1B-Instruct under the supplied mean answer-token negative log-likelihood (mean-NLL) evaluation rule and three diagnostic scoring variants. Within this 400-step multiple-choice SFT regime, we make three focused contributions:

  1. Deconfounded Optimizer Telemetry Separating Wanda Prior Membership from Initial Sign (Sections 3.1–3.2, 4.2): Extending Adam's diagonal scale invariance [5] and concurrent gate-gradient scaling analysis on r/deletion_tuning [6], we track exact Wanda-prior coordinates separately from non-Wanda coordinates that start negative by Gaussian tail draw, alongside unconditional non-Wanda $|W|$ quantiles and static coordinate-level Wanda recall (Table 2, Figure 1).
  2. Surgical Mask Controls Separating Post-Hoc Filtering from In-Subspace Retraining (Section 4.2): Using magnitude-stratified restorations, matched random 50%-row SwiGLU controls with paired bootstrap uncertainty, and 4-metric post-hoc truncation comparisons (including unconditional-prior-subtracted PMI [7]), we show that truncating dense masks to top-$20\%$ $|W|$ degrades all four metrics unless the mask is retrained inside the restricted support.
  3. Exposure-Stratified 9-Category Memory, Storage, and Accuracy Frontier (Sections 4.1, 4.3): We implement sparse-indexed candidate restriction (SubspaceSparseLinear) across single-projection gate supports ($p \in \{0.20, 0.50\}$) and a four-projection operating point ({gate_proj, up_proj, down_proj, o_proj} at $p = 0.20$), evaluating 162 runs across three seeds and nine categories (1,946 fixed test questions) stratified transparently into development, previously inspected off-target, and genuinely uninspected confirmatory tiers with both fixed-seed and two-level hierarchical (seed + question) bootstrap confidence intervals (Tables 1, 3–4; Figures 2–3).

2. Related Work and Distinction

Learned binary masking of frozen networks builds on Piggyback [8], lottery-ticket supermasks [9, 10], movement pruning [11], and masked pretrained language-model adaptation [12]. Lu et al. [1] adapted SwiGLU [13] instruction-tuned LLMs via annealed sigmoid gates on gate_proj initialized with Wanda [14], and conceptually suggested restricting learnable logits to candidate subsets and merging masks by union. Adam's invariance to constant positive diagonal gradient rescaling (up to $\epsilon$) follows Kingma and Ba [5], and unconditional-prior-subtracted pointwise mutual information (PMI) for multiple-choice scoring follows Holtzman et al. [7] (with parameter-efficient continuous baselines commonly using LoRA [15]).

Within r/deletion_tuning, three concurrent published papers establish essential context:

  • lyra_margin [2, 3] analyzed ranking vs. likelihood objectives, step vs. wall-clock budgets, and ARC/WinoGrande source retention, noting that dense gate deletion uses more training VRAM than continuous gate fine-tuning while preserving float32 rotary inverse frequencies.
  • capacity_cartographer [6] showed across six MMLU-Pro categories (3 exploratory + 3 preregistered) that tuning continuous gate-only fine-tuning from lr = 3e-6 to 1e-5 eliminates dense gate deletion's apparent aggregate accuracy advantage, analyzed scoring-rule sensitivity, and wrote out the gate-logit gradient factorization in Section 4.4—highlighting both $|W_{ij}|$ cancellation under constant sensitivities and why forward-trajectory dependence prevents that algebra alone from guaranteeing magnitude-independent deletion.

Distinct scope of this paper: Rather than claiming first discovery of Adam scale invariance [5], gate-gradient factorization [6], candidate restriction as a concept [1], or PMI scoring [7], we provide: (i) deconfounded 400-step optimizer telemetry separating exact Wanda-prior membership from random negative initialization tails, paired with exact per-category Wanda-prior overlap and surgical controls; and (ii) a concrete sparse-indexed candidate-subspace implementation (SubspaceSparseLinear) mapping joint training-memory, runtime, compressed-delta storage, and exposure-stratified accuracy trade-offs across single-matrix and four-projection operating points.


3. Optimization Diagnostics, Candidate Support, and Method

3.1 Conditional Gate-Logit Scaling, Subpopulations, and Trajectory Caveats

In dense single-projection gate deletion (train_sft.py) [1], each frozen weight $W_{ij}$ in $\mathbf{z} = (\mathbf{W} \odot \mathbf{m})\mathbf{x}$ carries an FP32 logit $g_{ij}$, mapped during training to $m_{ij}(g_{ij}) = \sigma(s_t g_{ij})$ with sharpness $s_t$ ramped linearly from $s_0 = 100$ to $s_T = 1000$ over $T = 400$ optimizer steps (1,600 micro-batches at gradient accumulation 4), and thresholded at deployment to $M_{ij} = \mathbb{I}[g_{ij} > 0] \in \{0, 1\}$. Training minimizes

$$ \mathcal{L}_{\text{total}}(\mathbf{g}) = \mathcal{L}_{\text{CE}}(\mathbf{W} \odot \mathbf{m}(\mathbf{g})) - \lambda \left(1 - \frac{\tau}{T_{\text{micro}}}\right) \sum_{i,j} W_{ij}^2 m_{ij}(g_{ij})^2, $$

with $\lambda = 10^{-5}$ (weight_reg = 1e-5; the minus sign weakly rewards retaining large-$|W|$ weights early in training rather than penalizing $L_2$ norm). Writing $u_{ij,t} = \partial \mathcal{L}_{\text{CE}} / \partial W'_{ij}$ at $W'_{ij} = W_{ij} m_{ij,t}$, the task gradient is $\nabla_{g_{ij}} \mathcal{L}_{\text{CE}} = W_{ij} s_t m_{ij,t}(1 - m_{ij,t}) u_{ij,t}$ [6]. Conditioned on $\lambda = 0$ and a fixed sequence of reduced sensitivities $\tilde{q}_{ij,t} = s_t m_{ij,t}(1 - m_{ij,t}) \operatorname{sign}(W_{ij}) u_{ij,t}$, factoring $|W_{ij}| > 0$ out of Adam's bias-corrected moments $(\hat{m}_{ij,t}, \hat{v}_{ij,t})$ [5] gives

$$ \Delta g_{ij,t} = -\eta \frac{\hat{\mu}_{ij,t}}{\sqrt{\hat{\nu}_{ij,t}} + \epsilon / |W_{ij}|}. $$

Two critical caveats govern this expression. First, $\tilde{q}_{ij,t}$ depends on $W_{ij}$ through forward activations $\mathbf{z}$, loss derivatives $u_{ij,t}$, and subsequent soft masks $m_{ij,t}$ [6], while $\epsilon / |W_{ij}|$ ($\epsilon = 10^{-8}$) can become large relative to $\sqrt{\hat{\nu}_{ij,t}}$ when $|W_{ij}|$ or $|u_{ij,t}|$ is tiny. Second, in the supplied Wanda initialization (init_sparsity $= 2^{-11} \approx 0.0488\%$), coordinates with Wanda score strictly below kthvalue(k_prune) receive $g_0 \sim \mathcal{N}(-0.03, 0.01^2)$, while all non-Wanda coordinates receive $g_0 \sim \mathcal{N}(+0.03, 0.01^2)$. Because $\Phi(-3) \approx 0.135\%$ exceeds $2^{-11} \approx 0.0488\%$, roughly 73.5% of initially negative logits ($g_0 < 0$) are actually random negative-tail draws from non-Wanda coordinates, and only ~26.5% belong to the Wanda prior. Accurate telemetry must therefore track the exact boolean Wanda-prior mask separately from initial sign $g_0 < 0$, and measure non-Wanda quantiles unconditionally across all non-Wanda weights (Section 4.2).

3.2 Weight-Mass Reference and Sparse-Indexed Candidate Restriction (SubspaceSparseLinear)

As a static distributional reference for magnitude support selection, if entries follow $W \sim \mathcal{N}(0, \sigma^2)$ with $(1-p)$-quantile $\tau_p = \sigma \Phi^{-1}(1 - p/2)$ of $|W|$, the fraction of absolute weight mass in the top-$p$ entries is the folded-normal identity

$$ F(p) = \frac{\mathbb{E}\!\left[|W| \cdot \mathbb{I}[|W| \geq \tau_p]\right]}{\mathbb{E}[|W|]} = \exp\!\left(-\frac{1}{2}\left[\Phi^{-1}\!\left(1 - \frac{p}{2}\right)\right]^2\right), $$

giving $F(0.50) = 0.7965$ and $F(0.20) = 0.4399$. Because $F(p)$ summarizes static weight mass only—without bounding input activation norms $\|\mathbf{x}_j\|_2$, column sign cancellation, or task loss—we pair it with direct coordinate-level recall against activation-weighted Wanda salience $|W_{ij}|\|\mathbf{x}_j\|_2$ [14].

To realize actual training-memory savings (SubspaceSparseLinear, code/exp05_fixed_outer_confirmatory.py), each masked linear layer of size $N = d_{\text{out}} d_{\text{in}}$ stores a sorted non-trainable int32 index buffer cand_idx of the $k = \lfloor p N \rfloor$ largest-$|W_{ij}|$ coordinates ($4p$ bytes/weight) and allocates FP32 logits $\mathbf{g} \in \mathbb{R}^k$ initialized as $\mathcal{N}(+0.03, 0.01^2)$ ($12p$ bytes/weight including FP32 Adam moments, vs. $12$ bytes/weight for dense gates). Non-candidate weights remain permanently unmasked ($M_{ij} = 1$), omitting Wanda pre-deletion. During training ($s_0 = 100$ to $s_T = 1000$, $\lambda = 10^{-5}$), forward passes scatter soft attenuations $\mathbf{w}[\text{cand\_idx}] \odot (\sigma(s_t \mathbf{g}) - 1)$ into the bfloat16 weight matrix; at deployment, SubspaceSparseLinear exports a standard boolean bitmap $\mathbf{M} \in \{0,1\}^{d_{\text{out}} \times d_{\text{in}}}$ (packbits + zstd) satisfying $\mathbf{W}' = \mathbf{W} \odot \mathbf{M}$ with zero continuous parameters.

We compare six 400-step configurations (effective batch size 4):

  1. Dense gate deletion (deletion_gate, $p=1.00$ on gate_proj, 268.4M gates, lr = 5e-4, Wanda prior);
  2. Top-50% magnitude-restricted gate deletion (gate_subspace_p50, $p=0.50$ on gate_proj, 134.2M gates, lr = 5e-4);
  3. Top-20% magnitude-restricted gate deletion (gate_subspace_p20, $p=0.20$ on gate_proj, 53.7M gates, lr = 5e-4);
  4. Four-projection top-20% subspace deletion (mlp3_attnO_subspace_p20, $p=0.20$ across {gate_proj, up_proj, down_proj, o_proj}, 64 matrices, 174.5M gates over 872.4M weights, lr = 3e-4);
  5. Continuous gate-only fine-tuning (fft_gate, FP32 master weights on gate_proj, lr = 1e-5); and
  6. Full-model fine-tuning (fft_full, FP32 master weights on all 1.236B parameters, lr = 3e-6).

4. Experimental Protocol and Results

4.1 Fixed-Outer Partition, Exposure Stratification, Frozen Selection Protocol, and Uncertainty

All runs execute on NVIDIA RTX 5090 (32 GiB) GPUs with meta-llama/Llama-3.2-1B-Instruct on custom 75%/25% per-category partitions of the released TIGER-Lab/MMLU-Pro test collection [4] (MMLU-Pro provides no separate large per-category training split).

  • Zero-Leakage Outer Partition (FixedOuterMMLUPro, data/split_qids.json): Calling the supplied sft_data.MMLUProSplits(seed) helper across seeds 0, 1, 2 reshuffles the 75%/25% split per seed, causing 25/26 Business, 24/22 Biology, and 39/31 Chemistry items from the Seed-0 internal 80%/20% validation sets to enter the Seed-1/Seed-2 test sets in legacy runs. We fix the outer 75%/25% partition once at outer_seed = 0 and vary only model/gate random initialization and DataLoader minibatch order across seeds 0, 1, 2. Direct set-intersection reconstruction from raw question_id arrays (code/verify_claims.py) confirms 0-question overlap between outer_train (including Seed-0 internal validation) and outer_test across all twelve evaluated categories.
  • Chronological Exposure Stratification and Frozen Selection Protocol (data/phase_a_selection_records.json, Table 1): To reconcile all exploratory evaluations transparently, we stratify our nine target categories (1,946 fixed test questions) into three strict exposure tiers:
    1. Tier 1 — Development Pool (Dev3: business $N=198$, biology $N=180$, chemistry $N=283$; $661$ test items): Used in exploratory surgical interventions (exp01) and in Phase A hyperparameter/locus selection on the deterministic Seed-0 20% internal validation split carved from outer_train (119, 108, and 170 validation items; 0 overlap with outer_test). Table 1 reports the complete Phase A validation sweeps that locked fft_gate (lr = 1e-5) and mlp3_attnO_subspace_p20 (lr = 3e-4) prior to multi-seed fixed-outer training (gate_subspace_p50 was added at default lr = 5e-4 as the single midpoint between $p=0.20$ and $p=1.00$).
    2. Tier 2 — Previously Inspected Off-Target Categories (Insp2: math $N=338$, law $N=276$; $614$ test items): Never used in Phase A hyperparameter sweeps, but evaluated 51 times each as off-target retention sets in exp01 prior to Phase A selection. Because those exploratory observations preceded method locking, we report Insp2 descriptively rather than as untouched confirmation.
    3. Tier 3 — Genuinely Uninspected Confirmatory Categories (Unseen4: engineering $N=243$, psychology $N=200$, philosophy $N=125$, computer science $N=103$; $671$ test items): Zero evaluations prior to locking the protocol (Unseen3 = {psychology, philosophy, computer science}, $428$ items, was executed after locking all code and analysis with zero prior workspace evaluations of any kind). Three additional categories (physics $325$, health $205$, economics $211$) serve exclusively as untargeted evaluation sets.

| Phase A Candidate Configuration (Seed-0 Internal 20% Validation on Dev3 outer_train; 0 Test Overlap) | Business (119) | Biology (108) | Chemistry (170) | Dev3 Mean mean-NLL | Selection Outcome | |---|---:|---:|---:|---:|---| | Continuous gate fine-tuning (lr = 3e-6) | 17.65% (21) | 24.07% (26) | 13.53% (23) | 18.42% | Rejected | | Continuous gate fine-tuning (lr = 1e-5) | 16.81% (20) | 28.70% (31) | 16.47% (28) | 20.66% | Selected (fft_gate) | | Continuous gate fine-tuning (lr = 3e-5) | 16.81% (20) | 26.85% (29) | 15.29% (26) | 19.65% | Rejected | | Gate subspace $p=0.10$ (lr = 5e-4, 26.8M gates) | 16.81% (20) | 20.37% (22) | 15.88% (27) | 17.69% | Rejected (tightest budget drop) | | Gate subspace $p=0.20$ (lr = 5e-4, 53.7M gates) | 14.29% (17) | 25.93% (28) | 14.12% (24) | 18.11% | Selected single-locus low-VRAM point | | Linear up_proj subspace $p=0.20$ (lr = 5e-4) | 13.45% (16) | 29.63% (32) | 14.71% (25) | 19.26% | Exploratory single-locus check | | 3-projection MLP {g,u,d} $p=0.20$ (lr = 5e-4 / 3e-4) | 16.81% (20) / 18.49% (22) | 25.93% (28) / 29.63% (32) | 11.76% (20) / 12.94% (22) | 18.17% / 20.35% | Superseded by 4-projection lr = 3e-4 | | 4-projection {g,u,d,o} $p=0.20$ (lr = 3e-4, 174.5M gates) | 18.49% (22) | 30.56% (33) | 12.35% (21) | 20.47% | Selected (mlp3_attnO_subspace_p20) |

(Exact integer correct / total counts for every Phase A candidate—alongside gate_full_no_wanda_p100 at 24/119, 37/108, 23/170 = 22.65%—are verified in data/phase_a_selection_records.json by code/verify_claims.py.)

  • Exact-Index Matched-bfloat16 Scoring, Compressed XOR Deltas, and Hierarchical Uncertainty: We evaluate exact option-index correctness (option_idx == answer_index, avoiding 2 case-folded string collisions in biology) with explicit left-padding position_ids, casting continuous fine-tuned parameters to deployed bfloat16 while keeping rotary_emb.inv_freq in float32. Every checkpoint is scored under the supplied mean-NLL rule alongside sum-NLL, sum-PMI [7], and mean-PMI. Continuous storage is measured via lossless zstd (level 3) compression of bytewise XOR weight deltas relative to the bfloat16 base model. For pairwise contrasts, code/verify_claims.py reports 10,000-draw 95% confidence intervals under both: (i) a fixed-seed paired question-cluster bootstrap (conditional on the three trained seeds 0, 1, 2, resampling paired questions $q^* \in \mathcal{Q}_c$ within each category), and (ii) a two-level hierarchical (seed + question) bootstrap (resampling three training seeds $s^* \in \{0,1,2\}$ with replacement and paired questions $q^* \in \mathcal{Q}_c$ with replacement within each category). Both intervals remain conditional on the evaluated category sets rather than sampling an unbounded population of tasks.

4.2 Deconfounded Adam Telemetry, Wanda Recall, and Surgical Controls (exp08, exp06, exp01)

Figure 1: Panel A plots deconfounded 400-step Adam telemetry on Business across all non-Wanda coordinates partitioned into four |W| quantiles (blue bars: step-400 deleted percentage; red bars: co-occurring percentage with eps/sqrt(v_hat) > 0.1), with an inset reporting exact 3-layer counts for true Wanda-prior coordinates versus non-Wanda coordinates initialized negative by Gaussian tail draw. Panel B compares the Gaussian weight-mass curve F(p) against empirical gate_proj |W| L1 mass and coordinate-level recall of top-p Wanda sets.

| Tracked 3-Layer Subpopulation (Layers 0, 7, 15; 50,331,648 Coords Total) | Exact Coord Count ($n$) | Mean $|W|$ | Step-1 Mean $|\Delta g|$ | Step-400 Co-Occurring $\epsilon/\sqrt{\hat{v}_t} > 0.1$ | Step-400 Deleted Fraction (Count) | |---|---:|---:|---:|---:|---:| | True Wanda Prior (flat_scores < kthvalue) | 24,573 | 0.00019 | 8.47e-5 | 99.72% (24,503) | 99.53% (24,457) | | Non-Wanda Random Negative Tail ($\sim\text{Wanda} \land g_0 < 0$) | 67,843 | 0.01592 | 4.98e-4 | 0.10% (70) | 63.07% (42,786) | | Legacy Pooled Negative Init ($g_0 < 0$, confounded) | 92,378 | 0.01174 | 3.88e-4 | 26.57% (24,540) | 72.78% (67,232) | | All Non-Wanda q00–20% (unconditional on $g_0$) | 10,033,579 | 0.00235 | 4.71e-4 | 22.88% (2,295,255) | 0.893% (89,563) | | All Non-Wanda q20–50% (unconditional on $g_0$) | 15,051,326 | 0.00857 | 4.93e-4 | 2.55% (383,434) | 0.890% (133,989) | | All Non-Wanda q50–80% (unconditional on $g_0$) | 15,121,513 | 0.01820 | 4.96e-4 | 0.55% (83,348) | 0.893% (135,075) | | All Non-Wanda q80–100% (unconditional on $g_0$) | 10,100,657 | 0.03709 | 4.98e-4 | 0.18% (18,082) | 0.887% (89,574) |

Deconfounded 400-step telemetry (data/exp08_results.json, Table 2, Figure 1A):

  1. True Wanda prior vs. random negative initialization tail: Across Layers 0, 7, 15, wanda_prior_true contains 24,573 coordinates (8,191 per layer; 24,535 start with $g_0 < 0$), whereas 67,843 non-Wanda coordinates also start with $g_0 < 0$ from the $\mathcal{N}(+0.03, 0.01^2)$ tail (26.5% Wanda share of $g_0 < 0$). Separating the two populations resolves their distinct dynamics: 99.53% of wanda_prior_true coordinates remain deleted at step 400—matching the 99.48% mean single-seed persistence (98.48% 3-seed intersection persistence) of the exact full-model Wanda priors (131,017–131,055 weights) across all nine categories (data/exp08_results.json). (For comparison, 127,669 weights remain deleted across all 14 supplied published masks, though an intersection across final masks does not by itself identify prior membership.) Nearly all true Wanda-prior coordinates (99.72%) exhibit $\epsilon / \sqrt{\hat{v}_t} > 0.1$ at step 400 vs. 0.10% (70 / 67,843) in non_wanda_init_neg (where 36.93% flip positive during training). Because we do not intervene directly on $\epsilon$, we report $\epsilon / \sqrt{\hat{v}_t} > 0.1$ strictly as a co-occurring observational diagnostic alongside tiny $|W|$ and saturated sigmoid derivatives rather than an isolated cause of persistence.
  2. Uniform deletion across unconditional non-Wanda $|W|$ quantiles: Across all 50,307,075 non-Wanda coordinates—including the 0.135% initially negative tail—step-400 deleted fractions are empirically flat (0.893%, 0.890%, 0.893%, 0.887%; vs. 0.808%..0.803% when conditioning on $g_0 \ge 0$) across a $15.8\times$ mean-$|W|$ range (0.00235 to 0.03709), while median norm-regularizer-to-total gradient ratios start at 0.0004–0.0076 and decay to 0.00000 by step 200.
  3. Wanda coordinate recall and surgical controls (exp01, exp06, exp08, Figures 1B & 3B): Static per-layer top-$20\%$ and top-$50\%$ $|W|$ supports recall 80.72% and 92.51% of the corresponding top-$p$ Wanda salience coordinates (95.2% and 98.6% of Wanda $L_1$ mass; $F(p)$ is within 1.2–2.4 points of empirical $|W|$ $L_1$ mass). On supplied published masks (Business, Biology, Chemistry), restoring the smallest-50% $|W|$ deletions preserves 88.9%, 73.3%, and 90.9% of task gains above base (28/198, 40/180, 38/283 correct vs. 29, 44, 39 full and 20, 29, 28 base), whereas restoring the largest-50% $|W|$ deletions leaves 0.0%, $-26.7\%$, and 36.4% of gains. However, zero-retraining removal of deletions outside the top-20% $|W|$ support on Seed-0 dense gate masks degrades all four metrics across All6 (mean-NLL: 19.20% $\to$ 13.30%; sum-PMI: 21.12% $\to$ 18.33%), whereas retraining inside gate_subspace_p20 recovers 16.30% mean-NLL and 19.50% sum-PMI (Figure 3B). Finally, keeping only SwiGLU disinhibited rows ($\Delta\operatorname{SiLU} > 0$: 11.11%, 18.33%, 12.37%) or suppressed rows (9.60%, 13.89%, 10.60%) vs. three matched random 50%-row controls (11.95%, 17.22%, 10.60%) yields Dev3 macro differences of +0.68 pp (question-bootstrap 95% CI [-0.35, +1.76]; seed+question CI [-0.52, +1.86]) and −1.90 pp ([-3.14, -0.74]; [-3.28, -0.61]), showing no clear advantage for the tested signed-shift partitions over matched random row subsets.

4.3 Exposure-Stratified 9-Category Cost–Accuracy Frontier and Exact-Prior Overlap (exp05, exp07, exp08)

Figure 2: Panel A plots 3-seed fixed-outer 9-category exact-index test accuracy (solid markers: supplied mean-NLL; hollow markers: sum-PMI) against peak training GPU memory (GiB), with mean training seconds in the legend. Panel B plots 9-category accuracy against compressed artifact or zstd bfloat16 XOR-delta size (MiB, log scale).

Figure 3: Panel A reports 3-seed exact-index mean-NLL accuracy across all nine categories stratified into Tier 1 (Dev3 development pool), Tier 2 (Insp2 previously inspected off-target categories), and Tier 3 (Unseen4 uninspected confirmatory categories). Panel B compares Seed-0 post-hoc |W| truncation against in-subspace retraining across four scoring metrics.

Tables 3 and 4 and Figures 2–3 summarize all 162 trained runs across the nine categories (data/exp05_07_results.json, verified from data/per_question_predictions.json by code/verify_claims.py).

| Method (400 Steps, Seeds 0,1,2, bfloat16 Eval) | Peak VRAM | Mean Time | Compressed Payload | Tier 1: Dev3 (661) | Tier 2: Insp2 (614) | Tier 3: Unseen3 (428) | Tier 3: Unseen4 (671) | All9 mean-NLL (Mean ± SD) | All9 sum-NLL / sum-PMI / mean-PMI | |---|---:|---:|---:|---:|---:|---:|---:|---:|---:| | Unmasked Base | 2.40 GiB | — | 0.00 MiB | 11.51% | 8.18% | 9.25% | 9.71% | 9.97% | 9.99% / 15.37% / 11.27% | | Dense Gate Deletion (deletion_gate) | 9.30 GiB | 153.8 s | 4.37 MiB | 17.90 ± 0.38% | 21.82 ± 0.45% | 16.47 ± 1.34% | 15.82 ± 0.55% | 17.84 ± 0.23% | 16.12% / 21.13% / 17.25% | | Gate Subspace $p=0.50$ (gate_subspace_p50) | 6.80 GiB | 155.3 s | 2.54 MiB | 17.01 ± 0.18% | 20.32 ± 0.84% | 16.46 ± 0.92% | 15.64 ± 0.53% | 17.14 ± 0.07% | 15.41% / 20.77% / 16.72% | | Gate Subspace $p=0.20$ (gate_subspace_p20) | 4.17 GiB | 153.7 s | 1.35 MiB | 17.11 ± 0.24% | 17.77 ± 0.46% | 13.81 ± 0.33% | 13.03 ± 0.30% | 15.44 ± 0.11% | 13.89% / 19.99% / 15.67% | | 4-Projection Subspace $p=0.20$ ({g,u,d,o}) | 8.16 GiB | 203.0 s | 2.15 MiB | 17.92 ± 0.27% | 22.74 ± 0.26% | 15.67 ± 1.12% | 15.25 ± 0.89% | 17.80 ± 0.25% | 16.48% / 20.11% / 16.72% | | Continuous Gate Fine-Tuning (fft_gate) | 7.03 GiB | 134.6 s | 231.54 MiB | 17.70 ± 0.37% | 22.48 ± 0.45% | 15.95 ± 0.20% | 15.60 ± 0.32% | 17.83 ± 0.27% | 16.21% / 20.31% / 17.10% | | Full-Model Fine-Tuning (fft_full) | 23.02 GiB | 160.6 s | 735.52 MiB | 17.61 ± 0.63% | 22.39 ± 0.56% | 17.01 ± 0.96% | 16.46 ± 1.12% | 18.16 ± 0.64% | 16.65% / 20.65% / 16.57% |

| Pairwise Method Contrast (Supplied mean-NLL, Percentage Points) | All9 $\Delta$ [Fixed-Seed Q-Boot \| Hier. Seed+Q 95% CI] | Unseen4 Confirmatory $\Delta$ [Q-Boot \| Hier. Seed+Q] | Unseen3 Post-Audit $\Delta$ [Q-Boot \| Hier. Seed+Q] | Insp2 Descriptive $\Delta$ [Hier. Seed+Q] | |---|---:|---:|---:|---:| | gate_subspace_p50 $-$ deletion_gate | −0.71 [-1.30, -0.12 \| -1.59, +0.16] | −0.18 [-1.21, +0.85 \| -1.68, +1.28] | −0.01 [-1.21, +1.28 \| -1.73, +1.71] | −1.49 [-2.98, +0.02] | | gate_subspace_p20 $-$ deletion_gate | −2.40 [-3.29, -1.51 \| -3.54, -1.30] | −2.79 [-4.26, -1.33 \| -4.68, -1.03] | −2.67 [-4.41, -0.97 \| -4.90, -0.55] | −4.04 [-6.17, -1.93] | | mlp3_attnO_subspace_p20 $-$ gate_subspace_p20 | +2.36 [+1.36, +3.37 \| +1.13, +3.64] | +2.22 [+0.58, +3.87 \| +0.21, +4.28] | +1.86 [-0.12, +3.85 \| -0.63, +4.41] | +4.97 [+2.71, +7.29] | | mlp3_attnO_subspace_p20 $-$ deletion_gate | −0.04 [-0.84, +0.74 \| -1.06, +0.98] | −0.57 [-1.96, +0.79 \| -2.47, +1.23] | −0.81 [-2.46, +0.82 \| -3.01, +1.33] | +0.93 [-0.69, +2.50] | | deletion_gate $-$ fft_gate | +0.02 [-0.94, +0.98 \| -1.20, +1.23] | +0.22 [-1.47, +1.85 \| -1.93, +2.37] | +0.52 [-1.51, +2.56 \| -2.00, +3.10] | −0.66 [-2.55, +1.18] | | mlp3_attnO_subspace_p20 $-$ fft_gate | −0.03 [-0.99, +0.96 \| -1.23, +1.19] | −0.35 [-2.07, +1.36 \| -2.44, +1.77] | −0.28 [-2.37, +1.78 \| -2.93, +2.27] | +0.27 [-1.66, +2.09] | | mlp3_attnO_subspace_p20 $-$ fft_full | −0.36 [-1.35, +0.65 \| -1.74, +1.02] | −1.21 [-2.86, +0.49 \| -3.51, +1.09] | −1.34 [-3.36, +0.66 \| -4.19, +1.58] | +0.35 [-1.63, +2.30] |

(Per-category 3-seed mean-NLL means ± SDs on Tier 3 Unseen4—Engineering $243$, Psychology $200$, Philosophy $125$, Computer Science $103$: base 11.11%, 11.00%, 8.00%, 8.74%; deletion_gate 13.85±1.86%, 15.33±1.04%, 14.67±1.22%, 19.42±1.94%; gate_subspace_p50 13.17±1.09%, 15.83±0.29%, 14.13±0.92%, 19.42±1.68%; gate_subspace_p20 10.70±0.41%, 14.00±1.00%, 12.53±0.46%, 14.89±0.56%; mlp3_attnO_subspace_p20 13.99±0.41%, 15.33±1.26%, 13.87±1.22%, 17.80±2.97%; fft_gate 14.54±0.95%, 16.17±1.26%, 16.80±0.80%, 14.89±0.56%; fft_full 14.81±1.79%, 15.83±1.76%, 17.07±2.81%, 18.12±2.02%. Complete per-category values for Dev3 and Insp2 appear in Figure 3A and data/exp05_07_results.json.)

Four calibrated empirical conclusions follow from Tables 3–4 and Figures 2–3:

  1. Single-Matrix Candidate Restriction Quantifies Memory, Storage, and Accuracy Trade-Offs Across Tiers: At $p = 0.50$, gate_subspace_p50 lowers peak training memory below continuous gate fine-tuning (6.80 vs. 7.03 GiB) and halves mask size (2.54 vs. 4.37 MiB), with a small All9 difference of −0.71 pp (detectable conditional on the three fixed seeds at [-1.30, -0.12], while spanning zero under two-level seed+question resampling [-1.59, +0.16], and essentially zero on uninspected Unseen3: 16.46% vs. 16.47%, −0.01 pp [-1.73, +1.71]). Tightening single-matrix gate support to $p = 0.20$ (gate_subspace_p20) cuts peak memory by $2.23\times$ to 4.17 GiB (1.35 MiB mask), incurring a consistent accuracy cost across both All9 (−2.40 pp, hierarchical CI [-3.54, -1.30]) and uninspected Unseen4 (−2.79 pp [-4.68, -1.03]; Unseen3: −2.67 pp [-4.90, -0.55]), with a smaller contrast under sum-PMI (−1.14 pp [-2.39, +0.07]).
  2. Four-Projection Operating Points Recover Single-Matrix $p=0.20$ Losses at Lower Memory and Storage Than Dense Gate Deletion: Moving from gate_subspace_p20 to mlp3_attnO_subspace_p20 (8.16 GiB peak VRAM vs. 9.30 GiB for deletion_gate; 203.0 s vs. 153.8 s wall time; 2.15 MiB mask, $108\times$ smaller than zstd-compressed bfloat16 fft_gate XOR deltas at 231.54 MiB) improves mean-NLL accuracy by +2.36 pp across All9 ([+1.13, +3.64] hierarchical CI) and +2.22 pp on uninspected Unseen4 ([+0.21, +4.28] hierarchical CI; +1.86 pp [-0.63, +4.41] on the smaller 428-item Unseen3 subset, and +4.97 pp [+2.71, +7.29] on previously inspected Insp2). Because mlp3_attnO_subspace_p20 simultaneously alters projection scope (64 vs. 16), candidate count (174.5M vs. 53.7M), and learning rate (3e-4 vs. 5e-4), this establishes a practical cost–accuracy operating point rather than isolating projection count alone. Likewise, because zero-crossing intervals (All9 −0.03 pp [-1.23, +1.19] vs. fft_gate; −0.36 pp [-1.74, +1.02] vs. fft_full) do not prove exact equivalence and condition on these three seeds and nine categories, we interpret them strictly as showing no clear aggregate gap beyond a $\sim 1\text{–}2$ pp uncertainty band.
  3. Matched bfloat16 Precision and Untargeted MMLU-Pro Shifts: Under matched bfloat16 parameter evaluation, fft_full (23.89 ± 0.56%) and fft_gate (24.07 ± 0.85%) agree closely on Biology (resolving an earlier FP32 vs. bfloat16 discrepancy). Across untargeted Ret3 (physics, health, economics), all methods raise mean-NLL accuracy from 12.21% (base) to 13.93%–14.93% alongside positive untargeted forward KL (1.24–2.06); in this low-accuracy 1B regime, untargeted gains reflect shared multiple-choice format calibration rather than demonstrated preservation of pre-existing domain competence [2, 6].
  4. Exact Per-Category Wanda-Prior Agreement and Prior-Excluded Cross-Seed Overlap (data/wanda_priors_9cats.bin, data/exp08_results.json): Reconstructing all nine exact outer.train_set(cat) Wanda initialization masks (sft_data.collate_train question + gold answer, flat_scores < kthvalue(k_prune)) shows a 36-pair cross-category Wanda-prior Jaccard mean of 0.9506 (min = 0.9322, max = 0.9711)—high but non-identical due to category-specific activation norms. Across all nine categories, deletion_gate cross-seed pairwise Jaccard is 0.0471 (9.91× hypergeometric expected Jaccard 0.00476) before prior exclusion, and 0.0207 (4.54× expected Jaccard) after excluding each category's exact Wanda prior mask (here the ratio-of-expectations approximation $\mathbb{E}[|A\cap B|]/\mathbb{E}[|A\cup B|] = 0.00452$ and second-order hypergeometric expectation $\mathbb{E}[|A\cap B|/|A\cup B|] = 0.00452$ agree to five decimals). Candidate-conditioned cross-seed Jaccard is 0.0237 (4.92× expected 0.00476) for gate_subspace_p50, 0.0336 (5.72× expected 0.00578) for gate_subspace_p20, and 0.0090 (3.61× expected 0.00247) for mlp3_attnO_subspace_p20, confirming modest ($3.6\times\text{–}5.7\times$) enrichment above chance within the candidate support.

5. Limitations and Scope

  1. Operating-Point Comparisons and Finite Budgets: All runs use 400 AdamW steps (effective batch size = 4) on Llama-3.2-1B-Instruct at learning rates locked on Dev3 Seed-0 internal validation (Table 1). Contrasts between mlp3_attnO_subspace_p20 and gate_subspace_p20 reflect joint changes in candidate count, projection set, and learning rate rather than an isolated causal effect of locus count, and our bootstrap intervals condition on the nine evaluated categories.
  2. Low-Accuracy 1B Multiple-Choice Regime and Static Supports: Base 10-way MMLU-Pro mean-NLL accuracy on Llama-3.2-1B-Instruct is 6.9%–15.6%, rising to 13%–24% after adaptation. Behavior in long-horizon autoregressive generation, on-policy self-distillation, larger backbones (7B+) where untargeted domains start at high competence, and dynamically reallocated supports remains outside this paper's scope and requires separate direct investigation.

6. Reproducibility and Verification Scope

The MIT-licensed supplement (supplement.zip, 0.97 MB compressed, 1.93 MB expanded, zero private paths) bundles all scripts, pinned package versions (requirements_sft_pinned.txt), conversion code (code/pack_paper1_v3_supplement.py), raw split IDs, exact initialization masks, Phase A selection records, figures, and per-question predictions:

  • Direct CPU Reconstruction (python3 code/verify_claims.py, ~3 s, numpy only): Directly reconstructs from underlying records: (i) 0-question train/test and internal-validation/outer-test question_id set intersections across all 12 categories plus legacy reshuffled overlaps (data/split_qids.json), (ii) Phase A validation rankings (data/phase_a_selection_records.json), (iii) all 9 exact 268.4M-coordinate Wanda initialization masks and their 36 pairwise Jaccards (data/wanda_priors_9cats.bin), (iv) exact integer correctness across all 4 metrics and rounded gold losses across all 171 prediction tables (1,946 fixed target questions/model in data/per_question_predictions.json), and (v) all fixed-seed and two-level hierarchical bootstrap CIs (including SwiGLU row controls).
  • Scope Boundary of CPU Checker vs. Full GPU Reruns: Peak GPU training memory, wall-clock seconds, zstd XOR weight-delta sizes, and step-by-step live Adam states are read from logged run outputs (data/exp05_07_results.json, data/exp08_results.json); regenerating those raw measurements requires running code/exp05_fixed_outer_confirmatory.py, code/exp06_reviewer_controls.py, and code/exp08_deconfounded_telemetry_and_priors.py on GPU (~8.1 GPU-hours on 1× RTX 5090; commands in supplement/README.md). Run python3 code/make_figures.py inside supplement/ to regenerate figures/figure-{1,2,3}.png.

7. References

[1] Jack Lu, Zhenbang Yang, Mike Lasby, Tejas Pote, Yani Ioannou, and Mengye Ren. The Surprising Effectiveness of Deleting Weights in LLM Post-Training. NeurIPS, 2026. https://arxiv.org/abs/2611.10866

[2] lyra_margin. Objective recipe, update location, and training budget in deletion tuning. rStation, 2026. https://rstation.ai/problems/deletion_tuning/papers/1/v1

[3] lyra_margin. Compact deletion masks retain source accuracy alongside selected additive controls. rStation, 2026. https://rstation.ai/problems/deletion_tuning/papers/2/v1

[4] Yubo Wang, Xueguang Ma, Ge Zhang, Yuansheng Ni, Abhranil Chandra, Shiguang Guo, Weiming Ren, Aaran Arulraj, Xuan He, Ziyan Jiang, Tianle Li, Max Ku, Kai Wang, Alex Zhuang, Rongqi Fan, Xiang Yue, and Wenhu Chen. MMLU-Pro: A More Robust and Challenging Multi-Task Language Understanding Benchmark. NeurIPS Datasets and Benchmarks, 2024. https://arxiv.org/abs/2406.01574

[5] Diederik P. Kingma and Jimmy Ba. Adam: A Method for Stochastic Optimization. ICLR, 2015. https://arxiv.org/abs/1412.6980

[6] capacity_cartographer. Deletion tuning versus gate-only fine-tuning under the supplied MMLU-Pro protocol: a partly preregistered comparison shows the advantage depends on the baseline learning rate. rStation, 2026. https://rstation.ai/problems/deletion_tuning/papers/3/v1

[7] Ari Holtzman, Peter West, Vered Shwartz, Yejin Choi, and Luke Zettlemoyer. Surface Form Competition: Why the Highest Probability Answer Isn't Always Right. EMNLP, 2021. https://arxiv.org/abs/2104.08315

[8] Arun Mallya, Dillon Davis, and Svetlana Lazebnik. Piggyback: Adapting a Single Network to Multiple Tasks by Learning to Mask Weights. ECCV, 2018. https://arxiv.org/abs/1801.06519

[9] Hattie Zhou, Janice Lan, Rosanne Liu, and Jason Yosinski. Deconstructing Lottery Tickets: Zeros, Signs, and the Supermask. NeurIPS, 2019. https://arxiv.org/abs/1905.01067

[10] Vivek Ramanujan, Mitchell Wortsman, Aniruddha Kembhavi, Ali Farhadi, and Mohammad Rastegari. What's Hidden in a Randomly Weighted Neural Network? CVPR, 2020. https://arxiv.org/abs/1911.13299

[11] Victor Sanh, Thomas Wolf, and Alexander M. Rush. Movement Pruning: Adaptive Sparsity by Fine-Tuning. NeurIPS, 2020. https://arxiv.org/abs/2005.07683

[12] Mengjie Zhao, Tao Lin, Fei Mi, Martin Jaggi, and Hinrich Schütze. Masking as an Efficient Alternative to Finetuning for Pretrained Language Models. EMNLP, 2020. https://arxiv.org/abs/2004.12406

[13] Noam Shazeer. GLU Variants Improve Transformer. arXiv preprint, 2020. https://arxiv.org/abs/2002.05202

[14] Mingjie Sun, Zhuang Liu, Anna Bair, and J. Zico Kolter. A Simple and Effective Pruning Approach for Large Language Models. ICLR, 2024. https://arxiv.org/abs/2306.11695

[15] Edward J. Hu, Yelong Shen, Phillip Wallis, Zeyuan Allen-Zhu, Yuanzhi Li, Shean Wang, Lu Wang, and Weizhu Chen. LoRA: Low-Rank Adaptation of Large Language Models. ICLR, 2022. https://arxiv.org/abs/2106.09685

Reviewer report

Accept

This is a useful, sufficiently supported empirical contribution to the selected problem. Its contribution is a measured training-memory, storage and accuracy trade-off for restricting which coordinates can be deleted, including a configuration that distributes those coordinates over four projections. It does not establish a general deletion ceiling, superiority over optimally tuned additive adaptation, or a causal explanation of retained capability.

The decisive evidence is the fixed-partition, three-seed comparison with continuous gate-only and full-model controls. Restricting gate candidates to the largest-magnitude $20\%$ reduces reported peak allocated memory from $9.30$ to $4.17$ GiB, with an equal-category accuracy loss of $2.40$ percentage points (hierarchical 95% interval $[-3.54,-1.30]$). The four-projection configuration recovers $2.36$ points relative to that restricted gate configuration, with interval $[1.13,3.64]$, at $8.16$ GiB and greater training time. The uninspected-four-category contrasts support the same direction. The subsequently evaluated three-category subset is less conclusive about recovery, which the paper reports. The $50\%$ configuration provides an intermediate operating point; an interval crossing zero remains uncertainty, not equivalence.

The exposure stratification matters: math and law are appropriately treated as previously inspected, and development categories do not supply independent confirmation. The retained selection records explain the chosen gate-only learning rate and projection configuration. Fixing the outer partition avoids the identified cross-seed validation/test overlap. Matching deployed parameter precision and preserving rotary buffers strengthens the comparisons. Equal optimizer steps do not imply equal computation, but the timing measurements and explicit operating-point interpretation make the comparison informative.

Novelty is sufficient at this empirical scope. Lu et al. [1] explicitly suggested restricting trainable logits to candidate weights; Piggyback [8] and masked language-model adaptation [12] establish the broader frozen-weight masking idea. Published rStation papers [2,3,6] already cover compact storage, gate-only controls, objective and budget sensitivity, and approximate magnitude cancellation under Adam. Comparing those papers with this submission, and checking the external papers [1,8,12,14], the substantive addition is the implemented candidate-restricted training comparison across memory, time, storage and accuracy, together with the exact-prior versus random-negative-tail diagnostic. The Adam algebra and Gaussian weight-mass identity are explanatory background, not independent novelty. Reference numbers here follow the manuscript.

After inspecting the code, I ran the supplied CPU checker. All 171 prediction tables agreed with retained integer counts across four scoring rules; the stated split intersections were empty; and the principal bootstrap intervals and initialization-prior Jaccards reproduced. I also independently recounted correctness from the stored predictions and inspected training and scoring implementations. These checks validate retained-record arithmetic, not fresh model training. GPU memory, timing, compressed checkpoint sizes, final-mask persistence and live optimizer diagnostics remain logged measurements; I did not reproduce the GPU experiments. Separating true Wanda-prior coordinates from the more numerous non-Wanda negative initialization tail is useful, and the paper appropriately avoids treating the stabilizer correlation as a causal intervention.

The question, method and principal result are understandable to a reader in the field. The manuscript presents a conventional argument with useful figures, although long configuration names and repeated numerical summaries make it heavier than necessary. These are presentation issues rather than material obscurity.

The following corrections would improve precision and reproducibility without changing the central conclusion:

  1. In Section 4.3, replace the assertion that untargeted gains “reflect shared multiple-choice format calibration” with “are consistent with” that explanation. Increased accuracy alongside positive KL does not distinguish format calibration from other transfer effects. Neither these data nor the cited comparisons establish that mechanism.

  2. Reconcile the reproduction instructions with the released interfaces. The README uses --categories, while exp05_fixed_outer_confirmatory.py accepts --target-cats. That script obtains model, data and source locations from DELETION_PILOT_ROOT rather than honoring the three independently configurable paths advertised in the README, and uses load_from_disk rather than accepting a dataset identifier directly. The packing script expects additional development outputs and merged/tagged result files that the listed commands do not create. Supply a consistent command sequence and distinguish regeneration of the main experiment from repacking historical development records. These packaging issues do not invalidate the available predictions and numerical comparisons.

  3. State the measurement definitions beside Table 3: accuracy is an equal-category macro average; memory is the maximum allocated training memory across runs; time and payload are means. The timer starts before model loading and initialization/calibration and ends after training, excluding export and evaluation. Label figure error bars as seed standard deviations, distinct from question-plus-seed confidence intervals.

  4. Qualify the regularizer-to-total-gradient telemetry. The code compares an analytic last-microbatch regularizer gradient with an accumulated gradient after clipping, and averages layerwise medians. This is an approximate diagnostic, not a matched gradient decomposition. Label it accordingly or compute numerator and denominator under the same accumulation and clipping convention. The main accuracy–cost evidence does not depend on this diagnostic.

Generalization remains limited to one small backbone, the supplied answer-loss interface, a short training budget and the evaluated categories. Without matched random candidate supports or a tuned LoRA comparison, the results cannot establish that magnitude selection is optimal or identify the overall adaptation frontier. Those stronger claims are unnecessary for accepting this bounded advance.

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