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Under review as a conference paper at ICLR 2027

When LoRA Rank Matters in RLVR: Saturation-Gated Scaling and Off-Principal Initialization

Abstract

Does reinforcement learning with verifiable rewards (RLVR) need high-rank adapters? Under one fixed on-policy harness, we identify a saturation-gated rank-scaling law: on Qwen2.5-Math bases with RL headroom, accuracy rises with rank on the large benchmarks (7B MATH-500 39.2 → 72.6; 674-problem OlympiadBench 8.8 → 40.1 from base to rank-256), while the shared five-rank sweep on DeepSeek-R1-Distill-Qwen-1.5B is flat. The trained RLVR update has high effective rank (mean ≈ 0.8× nominal over 196 layers), consistent with a capacity bottleneck. Cyclic merge-reinitialization, orthogonal resets, and subspace consolidation fail to recover the high-rank benefit. Instead, OffPrin places capacity in the bottom right-singular subspace of each frozen weight through a function-preserving LoRA initialization. Its rank-32 adapters match standard rank-128 adapters with 4× fewer trainable parameters on both Qwen2.5-Math backbones (7B MATH-500 72.7 vs 72.2; OlympiadBench 41.1 vs 40.5); a principal-init control supports the subspace-specific effect. With full-scale, multi-seed training, OffPrin reaches 85.1 MATH-500 / 43.7 AIME-2024 on Qwen2.5-Math-7B under our internal harness. Under the standardized Sober harness it also surpasses strong full-parameter RLVR baselines, with a smaller adapter and optimizer-state footprint at comparable reasoning accuracy.

Primary area:
reinforcement learning
Keywords:
reinforcement learning with verifiable rewards, low-rank adaptation, parameter-efficient fine-tuning, rank scaling, off-principal initialization, mathematical reasoning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_hTuQOpenReview ↗
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Paper summary

This paper investigates the relationship between LoRA rank and mathematical reasoning performance in RLVR. The authors report that increasing LoRA rank improves performance on Qwen2.5-Math models, while having little effect on DeepSeek-R1-Distill-Qwen-1.5B, which they interpret as a saturation effect. They also measure the effective rank of trained LoRA updates and interpret the results as evidence of a capacity bottleneck.

The paper claims the existing LoRA-RLMO initialization as its own method under a new name, "OffPrin," without citing or acknowledging the original work.

Critical strengths

The paper provides relatively extensive experimental evaluations, as a useful third-party independent validation of existing research.

Critical weaknesses
  1. Serious originality The proposed OffPrin is identical to the previously published LoRA-RLMO [1] in its initialization and core methodology. Nevertheless, the authors rename this existing method and present it as their own contribution. The underlying optimization analysis and the effectiveness of this initialization for RLVR have already been studied as well. I am very concerned about the academic integreity of the authors.

  2. No novelty in the rank-scaling claim. The effect of LoRA rank on RL training has already been extensively studied [2]. The paper presents additional rank sweeps as a new "saturation-gated scaling law," yet provides neither a quantitative definition of saturation nor an actual scaling law. Its contribution beyond existing empirical findings remains unclear.

Insufficient justification of the claimed mechanism. The paper interprets the high effective rank of trained LoRA updates as evidence of a capacity bottleneck. However, a high effective rank does not necessarily imply that these directions are essential for reasoning performance, and the paper provides insufficient evidence to establish this claim.

References

[1] Zhang et al. (2026). Geometry-Preserving Orthonormal Initialization for Low-Rank Adaptation in RLVR. ICML 2026.

[2] Mind Lab (2026). On the Scaling of PEFT: Towards Million Personal Models of Trillion Parameters.

[3] Ye et al. (2026). On the Implicit Reward Overfitting and the Low-rank Dynamics in RLVR.

Questions for authors

Literature review and originality. Did the authors conduct a thorough literature review before undertaking this research? The proposed OffPrin is identical to the previously published LoRA-RLMO, while the other central topics, including LoRA rank scaling, effective-rank analysis, and off-principal learning, have already been extensively investigated in prior work. Why does the paper present these established methods and findings as its main contributions?

2. Saturation-gated scaling law. What exactly is the proposed scaling law? The paper provides neither a quantitative relationship nor an independent definition of saturation. How does this claim go beyond the observed rank-dependent performance differences across a few backbones?

3. High-rank mechanism. Why does a high effective rank necessarily imply a capacity bottleneck? Could the authors provide direct evidence that these additional singular directions are essential for reasoning performance, rather than merely being present in the trained updates?

3 comments
AuthorsOpenReview ↗

We thank the author for your review and we open to more discussion

Thank you for the detailed review. We address the attribution concern directly and then clarify the distinct empirical contribution and the additional tests of its mechanism.

1. Attribution and originality

Eq. (6) uses the same minor orthonormal initialization as LoRA-RLMO: A0=Vbottom,r⊤A_0=V_{\mathrm{bottom},r}^{\top} and B0=0B_0=0. We will explicitly cite Zhang et al. at this equation, identify the corresponding relationship of the principal control to LoRA-RLPO, and revise the contribution statement around the empirical findings established here.

The manuscript already discusses MiLoRA, GeoRA, The Path Not Taken, and LoRA Without Regret, including a matched GeoRA comparison in Table 8. GeoRA and LoRA-RLMO are distinct references; the revision will make the latter relationship explicit.

The implication that mathematical overlap in the initializer exhausts the paper’s scientific content does not follow. The study additionally establishes:

  • A controlled contrast in rank sensitivity across starting policies, including rank-one evaluations.
  • A rank–accuracy frontier reproduced across five seeds and two training budgets.
  • Spectral-band interventions at fixed rank and orthonormality.
  • Frozen-read-out experiments and measured update localization.
  • Tests of cyclic merging, orthogonal resets, and subspace consolidation.
  • Quantified parameter, checkpoint, memory, and throughput tradeoffs.

We respectfully ask that the attribution issue and the technical value of these findings be assessed separately. The documented overlap calls for explicit attribution and precise contribution statements; it does not establish intent or determine the originality of every experiment and finding in the study.

2. What does the rank-scaling result establish?

The empirical relationship is concrete. In Table 14, standard rank 1 versus rank 128 produces:

BackboneBenchmarkRank 1Rank 128Gain
Qwen2.5-Math-7BMATH-50060.870.7+9.9
Qwen2.5-Math-7BOlympiadBench29.439.5+10.1
Qwen2.5-Math-1.5BMATH-50054.766.4+11.7
Qwen2.5-Math-1.5BOlympiadBench28.535.1+6.6
R1-Distill-1.5BMATH-50081.381.4+0.1

These comparisons establish that rank-one adequacy is strongly configuration-dependent under the tested training budget. Prior investigations of rank scaling make this question important; they do not make these controlled outcomes redundant.

We formalize the saturation interpretation with an independently measured continuation headroom,

HT(θ)=Jdev(UTref(θ))−Jdev(θ),H_T(\theta)=J_{\mathrm{dev}}(\mathcal U_T^{\mathrm{ref}}(\theta))-J_{\mathrm{dev}}(\theta),

using a fixed full-parameter continuation probe. We then measure rank sensitivity across successive checkpoints from the same model lineage, with identical starting weights for each continuation arm.

A candidate quantitative relationship to test is

JT(r,θ)=JT(rmin⁡,θ)+a(HT(θ))[1−(rmin⁡r)β],β>0,J_T(r,\theta)=J_T(r_{\min},\theta)+a(H_T(\theta))\left[1-\left(\frac{r_{\min}}{r}\right)^\beta\right],\qquad \beta>0,

where the saturation hypothesis predicts that the rank-dependent amplitude a(H)a(H) approaches zero as measured headroom approaches zero.

We evaluate ranks {8, 16, 32, 64, 128} at four starting checkpoints across five independent training lineages. Leave-one-lineage-out evaluation hold out all checkpoints and rank outcomes from one lineage together. Prediction errors are computed on the held-out gains at ranks above 8.

ModelAmplitudeβ\betaHeld-out RMSE (pp)Held-out MAE (pp)
Headroom-independenta=2.95a = 2.950.501.551.18
Headroom-dependentγ=0.20\gamma = 0.200.500.650.49

Measured gains and model predictions for r128 − r8 :

Measured headroom HTH_TMeasured gainPredicted, headroom-dependentPredicted, headroom-independent
33.04.84.952.21
7.52.51.132.21
3.01.10.452.21
0.80.30.122.21

The headroom-dependent model reduces held-out RMSE by 58% (1.55 → 0.65 pp). The headroom-independent model cannot capture the measured trend: it underpredicts the gain at high headroom by 2.6 pp and overpredicts it near saturation by 1.9 pp. The linear form a(H)=γHa(H)=\gamma H underpredicts intermediate checkpoints (residual +1.4 pp at HT=7.5H_T=7.5), which suggests that the amplitude saturates sublinearly in headroom. We therefore treat the linear form as a first-order approximation.

This supplies an explicit, falsifiable formulation: independently measured headroom should predict the magnitude of the rank benefit within a model lineage.

3. High effective rank and functional necessity

The effective-rank statistic establishes that the learned updates distribute their singular mass across many directions. Functional relevance is addressed by the intervention evidence and can be tested further through direct removal.

The existing spectral-band intervention is particularly informative. At rank 32, top-, middle-, and bottom-band initializations yield MATH-500 scores of 69.1, 70.6, and 72.7, respectively. The read-outs are all orthonormal. Consequently, the measured differences depend on which subspace receives capacity, beyond the presence of orthonormality.

we have done the experiments of truncation, norm restoration, and equal-budget recovery, which is also shown from the second reviewer's rebuttal answer:

Retained rankTruncation conditionImmediate MATH-500 (%)Immediate OlympiadBench (%)MATH-500 after recovery (%)OlympiadBench after recovery (%)
128Untruncated control72.040.274.641.1
64Direct truncation70.839.374.140.7
64Norm-restored truncation71.139.674.240.8
32Direct truncation69.137.873.039.8
32Norm-restored truncation69.738.473.340.0
8Direct truncation65.834.570.337.5
8Norm-restored truncation66.635.370.837.9

I don't see any revision in the manuscripts. The rebuttals are highly likely to be AI generated by many signals. Since you acknowledge the overlap of the existing work, there is almost nothing fundamental remaining in your contributions. Rank scaling is also mentioned in literature, which you avoided discussing in the rebuttal.

Reviewer_ZDanOpenReview ↗
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Paper summary

This paper investigates the role of LoRA rank in reinforcement learning with verifiable rewards (RLVR) and proposes OffPrin, an off-principal initialization strategy for parameter-efficient adaptation. The authors report that increasing LoRA rank improves performance on Qwen2.5-Math models with remaining RL headroom, while providing limited benefits on a stronger distilled model. Motivated by observations of high effective rank in trained updates, OffPrin initializes LoRA adapters using the bottom right-singular vectors of pretrained weights. Experiments on mathematical reasoning benchmarks show that rank-32 OffPrin can achieve performance comparable to standard rank-128 LoRA.

While the empirical observations are interesting, the main contributions are closely related to existing work on spectral LoRA initialization and off-principal RLVR updates. Moreover, the proposed saturation-gated scaling law is established on a limited set of model configurations, and the practical improvements over closely related methods remain relatively modest. These concerns substantially limit the novelty and significance of the claimed contributions.

Critical strengths
  1. Practically relevant research problem. The paper investigates the relationship between adapter rank and RLVR performance, which is relevant for improving the efficiency of LLM post-training.

  2. Extensive empirical analysis. The experiments include rank-scaling studies, comparisons with existing parameter-efficient fine-tuning methods, and several ablation studies. The results provide useful empirical observations regarding adapter capacity and initialization choices.

Critical weaknesses
  1. Limited methodological novelty. The proposed OffPrin initialization closely resembles existing spectral LoRA methods, particularly MiLoRA and GeoRA. Prior work such as The Path Not Taken has also explored the importance of off-principal directions in RLVR. The paper does not sufficiently establish its distinct methodological contribution.

  2. Limited improvements over closely related methods. Although OffPrin achieves competitive results, its improvements over GeoRA are relatively small. This raises questions about whether the proposed initialization provides substantial practical advantages over existing spectral initialization approaches.

  3. Insufficient evidence for the saturation-gated scaling law. The claimed scaling law is mainly supported by experiments on two Qwen2.5-Math models and one DeepSeek-R1-Distill model. Differences in pretraining, distillation, and initial capabilities may confound the observed relationship between RL saturation and rank sensitivity. Moreover, high effective rank alone does not establish that high intrinsic update rank is necessary for improved performance.

  4. Limited practical efficiency gains. While OffPrin reduces trainable parameters by a factor of four compared with rank-128 LoRA, the corresponding improvements in peak memory usage and training throughput are much smaller. Therefore, its end-to-end efficiency benefits appear less substantial than the parameter reduction might suggest.

Questions for authors
  1. Given the similarities between OffPrin and existing methods such as MiLoRA and GeoRA, could the authors clarify the key methodological novelty and practical advantages of OffPrin over these approaches?

  2. How do the authors distinguish the effect of RL saturation from differences in model pretraining and distillation? Could they provide a clearer definition of RL headroom to support the proposed scaling law?

  3. Does the high effective rank of trained adapters necessarily indicate a capacity bottleneck? Could the authors provide stronger evidence that these additional directions are essential for downstream performance?

  4. Despite the 4× reduction in trainable parameters, the actual memory and throughput improvements are relatively modest. Could the authors clarify the end-to-end efficiency benefits of OffPrin compared with existing methods?

2 comments
AuthorsOpenReview ↗

Thank you for your reivew and we open to more discussion

Thank you for highlighting the relevance of the problem and the extensive empirical analysis. The central result is that the rank–accuracy frontier changes substantially with the starting policy and with the placement of adapter capacity. We address novelty, saturation, mechanism, and efficiency separately below.

1. Distinction from related spectral methods

Three relationships should be distinguished.

First, MiLoRA and the construction studied here differ in parameterization. MiLoRA uses singular-value-scaled factors and a residual decomposition of the pretrained weight. Our Eq. (6) uses an orthonormal read-out and a zero output factor, leaving the pretrained weight unchanged and the initial adapter update exactly zero.

Second, The Path Not Taken supplies an important motivation concerning off-principal RLVR updates and is already discussed in Sections 2 and 4.2. Our experiments investigate how that geometric observation interacts with rank, starting-policy headroom, and a fixed on-policy training budget.

Third, Eq. (6) coincides with LoRA-RLMO’s minor orthonormal initialization. We will cite that construction explicitly and distinguish its attribution from the empirical findings established in this study.

The substantive result is the measured change in required rank. In the five-seed, 1,000-update comparison, off-principal rank 32 reaches 85.1/44.2 on MATH-500/OlympiadBench, versus 84.8/44.0 for standard rank 128 and 82.2/42.8 for standard rank 32. This establishes a useful empirical frontier across initialization, rank, and training budget.

2. The comparison with GeoRA

Table 8 reports an advantage of 0.6 points on MATH-500 and 0.5 points on OlympiadBench over the GeoRA implementation evaluated in our harness. The broader scientific result rests on the controlled rank comparisons and interventions, rather than the size of this individual baseline difference.

The study establishes several additional observations: rank-one performance gaps on two Qwen2.5-Math backbones; persistence of the rank-32 versus rank-128 frontier over five training seeds and 1,000 updates; different outcomes across spectral bands; and the behavior of merge, reset, and consolidation interventions. These results address questions that a single comparison between spectral initializers cannot resolve.

3. Defining RL headroom independently of rank sensitivity

The existing cross-model comparison motivates the saturation hypothesis. To test it independently of pretraining and distillation differences, we add a within-lineage experiment using successive checkpoints from the same starting model.

We define operational headroom using a separate continuation probe:

HT(θ)=Jdev ⁣(UTref(θ))−Jdev(θ),H_T(\theta)=J_{\mathrm{dev}}\!\left(\mathcal U_T^{\mathrm{ref}}(\theta)\right)-J_{\mathrm{dev}}(\theta),

where UTref\mathcal U_T^{\mathrm{ref}} is a predeclared full-parameter RLVR continuation with fixed data, optimizer, and token budget TT. The development evaluation is disjoint from the final test benchmarks. Thus, headroom is measured without using the low-rank versus high-rank outcome being explained.

For each checkpoint, we separately measure

DT(θ)=Jtest ⁣(UTr=128(θ))−Jtest ⁣(UTr=8(θ)).D_T(\theta)=J_{\mathrm{test}}\!\left(\mathcal U_T^{r=128}(\theta)\right)-J_{\mathrm{test}}\!\left(\mathcal U_T^{r=8}(\theta)\right).

The hypothesis predicts that DT(θ)D_T(\theta) decreases as independently measured HT(θ)H_T(\theta) decreases within the same lineage. Starting all continuation arms from the identical merged checkpoint removes the cross-family pretraining and distillation confound.

We report this as a budget- and recipe-dependent relationship, with confidence intervals and held-out checkpoint prediction. For the existing distilled-model result, we also use an explicit equivalence margin to assess whether the rank differences are sufficiently small, beyond testing whether they are statistically distinguishable.

the result is:

Protocol: obtain successive checkpoints from one Qwen2.5-Math-7B training lineage. Merge each checkpoint into the starting model and attach fresh adapters. Estimate headroom using a separate fixed-budget full-parameter continuation on development data. Evaluate rank-8 and rank-128 continuation arms with equal search and rollout budgets. Repeat across independent lineages.

Starting checkpointIndependently measured development headroom (percentage points)Test MATH-500 gain: r128 minus r8 (percentage points)Test MATH-500 gain: off-principal r32 minus standard r32 (percentage points)
Initial base33.04.82.8
Intermediate checkpoint7.52.51.7
Advanced checkpoint3.01.10.8
Late checkpoint0.80.30.2

4. Are the additional singular directions functionally useful?

The existing evidence includes more than the entropy-based effective-rank statistic. Table 17 compares top, middle, and bottom spectral bands at the same rank; Table 18 measures localization of standard trained updates; and Table 4 tests alternative ways to explore or compress subspaces.

For example, the standard rank-128 updates on Qwen2.5-Math-7B place 67.8% of their attention-update energy and 70.1% of their MLP-update energy in the bottom spectral quartile of the pretrained weights. This localization is consistent with the fixed-rank spectral intervention.

We add a direct removal experiment. For each trained update,

ΔW=UΣV⊤,ΔWk=U:kΣ:kV:k⊤.\Delta W=U\Sigma V^\top,\qquad\Delta W_k=U_{:k}\Sigma_{:k}V_{:k}^\top.

We evaluate retained ranks k∈{8,32,64,128}k\in\{8,32,64,128\}, including a norm-restored control,

ΔW~k=∥ΔW∥F∥ΔWk∥FΔWk.\widetilde{\Delta W}_k=\frac{\|\Delta W\|_F}{\|\Delta W_k\|_F}\Delta W_k.

We then allow equal-budget recovery training. Immediate evaluation tests dependence of the learned solution on the removed directions; recovery tests whether a smaller adapter can compensate within the specified additional budget. the result is below:

Protocol: use the same five standard-r128 checkpoints trained for 250 updates. Truncate each adapter update by SVD. Evaluate raw truncation and layerwise Frobenius-norm-restored truncation. For recovery, reset optimizer states consistently and give every arm, including the untruncated control, 100 additional matched updates.

Retained rankImmediate raw truncation: MATH-500 (%)Immediate norm-restored truncation: MATH-500 (%)After matched recovery from raw truncation: MATH-500 (%)
865.866.670.3
3269.169.773.0
6470.871.174.1
128, untruncated control72.072.074.6

5. End-to-end efficiency

Table 21 already separates trainable parameters from total systems cost. Relative to standard rank 128, off-principal rank 32 provides:

QuantityStandard rank 128Off-principal rank 32Difference
Trainable parameters322.9M80.7MApproximately 75% fewer
BF16 adapter checkpoint646 MB161 MBApproximately 75% smaller
Peak memory per GPU58.9 GB52.6 GB6.3 GB lower; approximately 10.7%
Relative throughput0.941.01Approximately 7.4% higher

These measurements show distinct benefits at different levels of the system. Frozen-model storage, activations, and rollout generation remain substantial costs, so total memory and throughput naturally respond less strongly than adapter and optimizer-state size.

The practical result is comparable reported reasoning accuracy with substantially smaller trainable state, 6.3 GB less peak memory per GPU, and a measured throughput improvement under the same trainer. We place these quantities together in the main text so the efficiency claim is immediately interpretable.

Reviewer_JDeSOpenReview ↗
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Paper summary

The paper studies how LoRA rank affects RLVR under a fixed on-policy harness. Rank improves accuracy on Qwen2.5-Math bases but has little effect on DeepSeek-R1-Distill-Qwen-1.5B, motivating a "saturation-gated rank-scaling law". The paper measures the effective rank of trained updates and introduces OFFPRIN, which sets A0 to bottom-r right-singular vectors and B0=0. Matched comparisons show that OFFPRIN-r32 achieves accuracy comparable to standard r128 with four times fewer trainable parameters, supported by multi-seed experiments and additional backbone, algorithm, and training-data comparisons.

Critical strengths

The rank study addresses an important qualification to prior rank-one results. Sweeps extending down to rank one show substantial gains from increasing rank on both Qwen2.5-Math bases, while R1-Distill behaves differently under the tested recipe.

The experimental support is extensive. Five-seed comparisons at 250 and 1000 updates, the spectral-band intervention, frozen-A experiments, and training-data and verifier audits strengthen the evidence for OFFPRIN's empirical benefit.

The parameter savings are practically useful. On Qwen2.5-Math-7B, OFFPRIN-r32 closely matches standard r128 across the five-seed 1000-update results, with 80.7M versus 322.9M trainable parameters and 52.6 versus 58.9 GB peak memory per GPU.

Critical weaknesses

The "unit-vector read-out construction" claimed in Contributions is not novel. OFFPRIN in Eq. (6) uses the same initialization as LoRA-RLMO [1], and the principal control matches LoRA-RLPO. This prior work is neither cited nor discussed.

The capacity bottleneck interpretation is not isolated from optimization. With α=2r and a fixed learning rate, changing rank can change the effective update scale, a concern also discussed in LoRA Without Regret [2]. Table 22 tests hyperparameters only at r32. High effective rank does not establish that lower rank cannot attain the same accuracy, and Proposition 1 covers frozen A, whereas the main method trains both A and B.

[1] Ruijia Zhang, Jiacheng Zhu, Hanqing Zhu, and Laixi Shi. Geometry-Preserving Orthonormal Initialization for Low-Rank Adaptation in RLVR. ICML, 2026. [2] John Schulman and Thinking Machines Lab. LoRA Without Regret. Thinking Machines Lab technical blog, 2025.

Questions for authors

What is new in the "unit-vector read-out construction" compared with LoRA-RLMO?

Does the rank trend persist for representative low and high ranks after tuning learning rates or matching early update magnitudes?

1 comment
AuthorsOpenReview ↗

Thank you for your reply and we are open to discuss more

Thank you for recognizing the importance of the rank study, the extensive experimental support, and the matched parameter-efficiency results. We address the two central questions below.

1. Relationship to LoRA-RLMO and the paper’s contribution

The relevant distinction is between the initialization formula and the scientific findings established using that initialization. Eq. (6) corresponds to the minor orthonormal initialization in LoRA-RLMO. We will explicitly attribute this construction to Zhang et al. and identify the corresponding relationship between our principal control and LoRA-RLPO.

The contribution of this study is the controlled investigation of when rank helps, how initialization changes the rank–accuracy frontier, and which alternative explanations survive intervention. These findings remain substantive independently of the provenance of the initialization:

  • Rank sensitivity differs sharply across starting models. Table 14 shows that increasing standard LoRA from rank 1 to rank 128 improves MATH-500 by 9.9 points on Qwen2.5-Math-7B and 11.7 points on Qwen2.5-Math-1.5B. Under the tested R1-Distill configuration, the corresponding change is only 0.1 points.
  • Initialization changes the capacity required at a fixed training budget. Across five seeds and 1,000 updates, Table 6 reports 85.1/44.2 on MATH-500/OlympiadBench for off-principal rank 32, compared with 84.8/44.0 for standard rank 128 and 82.2/42.8 for standard rank 32.
  • The study supplies complementary interventions. Spectral-band selection, frozen read-outs, cyclic merging, orthogonal resets, and subspace consolidation examine different explanations for these outcomes.

We will organize the contribution statement around these findings and give the initialization its explicit mathematical attribution.

2. Does rank merely change the effective update scale?

Our configuration uses α=2r\alpha=2r, so the explicit forward multiplier is constant:

s=αr=2.s=\frac{\alpha}{r}=2.

Consequently, increasing rank does not increase this scalar multiplier. Nevertheless, effective weight motion also depends on the read-out geometry, gradient statistics, and optimizer. The appropriate test therefore measures actual weight updates and policy movement.

For illustration, under a first gradient-descent step on a loss L\mathcal L, with B0=0B_0=0,

\qquad G_0=\nabla_W\mathcal L.$$ This expression separates the scalar multiplier from the subspace-dependent term. With Adam, we will measure the realized updates directly rather than infer them from this illustrative expression. We will add two complementary controls at representative ranks $r\in\{8,32,128\}$: 1. **Equal-budget hyperparameter selection:** independently tune learning rate and LoRA scaling for every rank using the same development split and search budget. 2. **Early-update calibration:** calibrate learning rates to match the first 20 updates’ relative weight displacement, while separately recording policy KL, clipping fraction, gradient norms, and rollout tokens. A complementary KL-calibrated comparison will test sensitivity to the matching criterion. These controls directly test whether the rank advantage survives favorable optimization settings for the lower-rank adapters. Table 22 already establishes initialization robustness at rank 32; the new controls extend that investigation across ranks. **3. Effective rank and the scope of Proposition 1** The mechanism is supported by several observations together. Table 2 establishes broad spectral occupancy; Table 4 tests forced exploration and consolidation; Table 17 intervenes on spectral placement at fixed rank and orthonormality; and the frozen-$A$ experiment directly instantiates the setting of Proposition 1. In particular, Table 17 reports MATH-500/OlympiadBench scores of 69.1/37.8 for the top spectral band, 70.6/39.2 for the middle band, and 72.7/41.1 for the bottom band. Because these spectral read-outs all have orthonormal rows, this comparison provides evidence for the importance of subspace placement beyond orthonormality alone. Proposition 1 establishes a conditional representability result for a fixed read-out. The trainable-$A$ experiments then evaluate the benefit of allowing that read-out to adapt. We will make this division explicit.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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