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Under review as a conference paper at ICLR 2027

When Does Per-Token Halting Help? Adaptive Token-Wise Damping for Fixed-Point Reasoning Models in Looped Transformers

Abstract

Fixed-Point Reasoning Models (FPRM) use a parameter-free halting rule based on the maximum token residual. A single slow-converging token can therefore keep an entire sequence active. We introduce Adaptive Token-Wise Damping (ATWD), which adapts damping independently at each token and periodically restores every token's initial step-size. This refresh guarantees bounded intervals between full-strength updates while iteration continues; it does not establish dynamical stability or reduce shared-block evaluation cost. Across three tasks, ATWD's benefits depend on the setting. Under causal attention, ATWD improves mean accuracy and observed cross-seed stability on the alternating group , but on the harder symmetric group it fails to reach the baseline's late generalization transition within the matched training budget. Scalar-shaped replays show rapid residual convergence; separate prediction diagnostics suggest low-diversity collapse. On bidirectional Sudoku, ATWD exceeds a hard-freeze-training ablation on sequence accuracy in all three seeds tested (+25.5% relative in the ratio of means), but trails the scalar baseline in mean accuracy and cross-seed stability. Because this ablation changes both training-time decay and refresh, it does not isolate refresh's causal contribution. The hard-freeze-trained models also produce fewer duplicate-constraint violations among their incorrect grids, revealing a trade-off between exact solution accuracy and this measure of failure severity. These results identify task-dependent benefits and limitations of token-wise damping, while distinguishing numerical convergence from solution correctness.

Primary area:
neurosymbolic & hybrid AI systems (physics-informed, logic & formal reasoning, etc.)
Keywords:
looped transformers, fixed-point iteration, adaptive computation, algorithmic reasoning, token-wise halting, test-time compute, mechanistic analysis

Reviews

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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_ReMuOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

The paper proposed Adaptive Token-Level Damping for Fixed point reasoners. It sets independent update step-sizes for each token.

Critical strengths

The modification is simple. The paper provides a bounded-staleness guarantee for its periodic refresh mechanism.

Critical weaknesses

W1. Poor presentation and insufficient checking for AI hallucinate.

  • fig2 is unreadable.
  • Table 2 is at different scale from Table 1&3. It is a minor problem but it is conflict to human habits.
  • the caption of Table 9 in appendix refers to Arm(4). however, the table only contains 1~3.

W2. Lack of novelty for the proposed algorithm.

  • Token-level adaptive computation or early stopping are well known ideas in looped transformers and the. fixed point reasoner is kind of looped transoformer. The paper should clarify which difficulties are specific to fixed-point reasoners and how the proposed algorithm addresses them.

W3. The experiment is insufficient.

  • The scope is restricted to A5/S5 toy experiments and most looped transformer can support real world math problems like GSM/AIME. Also, results in S5 fails to show the effectiveness of the proposed algorithm.
Questions for authors

See weakness.

1 comment
AuthorsOpenReview ↗

Response to Reviewer ReMu

Thank you.

W1 (presentation). The length-generalization (Fig. 2) and eval/steps (Fig. 3) figures were regenerated at readable font sizes. The violations figure (Fig. 5) now matches Table 3. Table 2 now spans the column width. The Table 9 caption error is fixed. All numbers were re-checked against logged values, and the revision adds the numeric tables.

W2 (novelty). We do not claim novelty for token-level adaptive computation, and the related-work text now says so. In fixed-point reasoners there is no learned exit gate. The shared quantity is the damping step-size, driven by the slowest token. ATWD decouples that, and the controls we ran show the benefit is not unique to it.

W3 (scope). We agree. The limitations now state that results are on small synthetic tasks and one puzzle benchmark. Settings such as GSM8K are out of scope, and S5 shows no benefit.

Reviewer_mAqAOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper introduced adaptive token-wise damping for fixed-point reasoning models, which replaced the scalar sequence-level damping step-size with independent per-token step-sizes and a periodic refresh mechanism every R iterations. The authors provided a scheduling bound on step-size staleness and evaluated ATWD across causal permutation state tracking and bidirectional 9x9 Sudoku. Empirical results illustrated that, although ATWD could improve length generalization and seed stability on specific types of tasks, it still suffered from low-diversity collapse and trailed the unmodified scalar baseline in both mean accuracy and cross-seed stability on Sudoku.

Critical strengths
  1. The paper intended to address a practical limitation of sequence-level halting in looped Transformers by proposing a simple, parameter-free per-token damping mechanism to avoid adding learned routing gates.

  2. Experimental results on the A_5 causal state-tracking task showed that ATWD improved 128-length sequence accuracy and reduced cross-seed variance compared to the scalar baseline.

Critical weaknesses
  1. Albeit the introduction mentioned the contribution around per-token halting and avoiding full-sequence compute bottlenecks, ATWD neither halts individual tokens early nor saves any computation, and Eq. (5) actually damps stagnating tokens while leaving already-converged tokens undamped.

  2. Proposition 3.1 is a trivial consequence of modulo arithmetic on a deterministic counter and provides no dynamical stability or fixed-point convergence guarantees for the coupled self-attention map.

  3. The core Sudoku ablation comparing ATWD against Hard-Freeze is confounded, as it changes both the training decay rate and the refresh period simultaneously, while omitting the necessary matched-decay, no-refresh control mentioned in Table 9.

  4. The Hard-Freeze ablation introduced a severe train-evaluation mismatch by employing instantaneous freezing during 72-step training runs but switching to gradual decay during 1,000-step evaluations, undermining conclusions about premature commitment.

  5. The empirical validation is weak overall, as ATWD completely fails to generalize on S_5 and underperforms the scalar baseline on Sudoku, while the S_5 mechanistic failure analysis in Appendix A.4 relies on unauthenticated scalar-shaped replays and unpreserved prediction logs.

Questions for authors
  1. On S_5, patience is increased to P=10 while refresh remains fixed at R=20, meaning a token can decay at most once before being reset to 1.0 at iteration 20. How could ATWD cause catastrophic mode collapse if step-sizes remain pinned at or near 1.0 throughout the solver loop?

  2. Why do the duplicate-constraint violation numbers in Table 3 differ from the values plotted in Figure 5, and why did the offline EMA checkpoint audit yield different solved counts from the logged W&B evaluations?

  3. Have the authors explored true per-token halting, such as freezing key-value states and skipping MLP updates once a token's residual remains below τ\tau for P iterations, to achieve actual FLOPs and wall-clock reductions?

  4. It would be nice to validate whether damping tokens only after they converge, or combining per-token damping with Jacobian spectral regularization, prevents the low-diversity collapse observed on S_5 and the variance inversion on Sudoku.

1 comment
AuthorsOpenReview ↗

Response to Reviewer mAqA

Thank you. We made the following changes.

W1. We agree that ATWD neither halts tokens early nor saves computation. The title and framing now say so, and Section 6.3 states it.

W2. The proposition is now called elementary, and the text states it gives no dynamical-stability guarantee.

W3 (confounded ablation). We ran the missing matched-decay, no-refresh arm on Sudoku (seed 0). It scores 0.274, against ATWD 0.271 and hard-freeze 0.190. Refresh adds nothing measurable there, so the premature-commitment motivation for refresh is unsupported on this task, and the paper now says so. This is one seed only.

W4 (train/eval mismatch). The mismatch (δ_train=0, δ_eval=0.99) is stated in the protocol and limitations. The arm does not test commitment at inference time. We did not run an evaluation-time hard-freeze arm.

W5 (weak validation, S5). The S5 mechanism evidence is still limited. The cross-evaluation uses the native checkpoints, and it places the failure in the weights, as detailed in our reply to Reviewer 4Uap (Q4). The replay evidence remains labelled as unauthenticated.

Q1. We added a remark (Remark 3.2) showing that, with refresh, the applied step-size is at least η0·δ^⌊(R−1)/P⌋. That is 0.95 for the S5 training settings. We then ran a no-damping control on A5: sequence accuracy 0.895 on seed 1 (ATWD 0.891, baseline 0.308), so little or no damping works on A5. Whether the S5 collapse comes from near-undamped training is untested, since no S5 control was run. We say so.

Q2. Figure 5 was regenerated directly from the Table 3 numbers so the figure and table now match exactly (with the x-axis label fixed to R=20). The differences between the first audit, the repeat audit, and the logged evaluations are at most 3 of 800 puzzles each. A plausible cause is batch-dependent evaluation halting, which we did not isolate. The appendix (Sections A.11 and A.15) lists all three sets of counts.

Q3 and Q4. True per-token halting with state freezing, and combination with Jacobian regularization, are stated as future work. We ran neither.

Reviewer_4UapOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
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Paper summary

The paper modifies the damped fixed-point solver of Fixed-Point Reasoning Models (FPRM), which halts a sequence once the maximum per-token relative residual falls below τ (Eqs. 1–2), so that a single slow token keeps the whole sequence iterating. Adaptive Token-Wise Damping (ATWD) replaces FPRM's single, sequence-level damping step-size with per-token step-sizes. Each decays by δ when its token's residual has stopped improving for P iterations while still above τ (Eqs. 4–6). An unconditional refresh every R iterations resets all per-token states (Eq. 7). Proposition 3.1 ("Bounded Staleness") states that no token goes more than R − 1 iterations without a reset to the initial step-size. Halting itself remains a sequence-level reduction (batch-level in evaluation), and every token is still processed at every iteration, so ATWD does not reduce compute (Sec. 6.3). ATWD beats a hard-freeze training ablation on every seed but trails the scalar baseline (Tables 2 and 6). Hard-freeze models make fewer duplicate-constraint violations (Table 3). The appendices add pseudocode, correctness tests, S5 replays, and a proposed factorial ablation.

Critical strengths

Overall motivation make sense. And the reporting is unusually transparent and self-critical, which makes the evidence understandable.

Critical weaknesses
  1. ATWD does not act on the problem that motivates it, and the title misdescribes the method. The abstract and introduction motivate the work with FPRM's max-residual halting rule: "one lagging token forces every other, already-converged token to keep iterating at full cost – the gap this paper addresses" (L. 075–077; also L. 013–015). ATWD leaves this rule unchanged. Halting is still the sequence-level maximum of Eq. 2, which the evaluation path further reduces across the batch (L. 154–156, 352). The shared block still evaluates every token at every iteration (L. 429–432). A token whose residual is below τ never has its step-size decayed (L. 174–177), so converged tokens keep iterating at their current step-size. The paper acknowledges that ATWD does not reduce shared-block cost (L. 016–018; Sec. 6.3). It also calls the method "a parameter-free, token-wise damping rule …, not a learned exit policy" (L. 082–083). Yet the title asks "When Does Per-Token Halting Help?". The Fig. 1 caption speaks of "Per-token adaptive halting" (L. 066), and Sec. 4.3 labels only the baseline as "sequence-level halting" (L. 268–269, 283–284). The Ethics Statement describes the work as "a mechanistic study of a halting rule" (L. 490). The term "per-token halting" is never defined. No experiment is designed to test whether ATWD makes sequences halt earlier, and the iteration counts that are reported show no reduction.

  2. The evidence does not establish an ATWD-specific benefit over the unmodified solver. The conclusion states that "ATWD's benefits are real but task-dependent" (L. 451). The only task on which ATWD beats the scalar baseline in the mean is A5, and that gain rests on three seeds per arm. Baseline sequence accuracies are 0.930, 0.308, and 0.058, versus 0.976, 0.891, and 0.978 for ATWD (L. 304–305). The best baseline seed thus exceeds the worst ATWD seed. The mean gap comes from two baseline seeds that generalize poorly to length 128, under a training schedule the authors cut for compute reasons (L. 245–246).

On S5, ATWD fails on both seeds (L. 314–316). On Sudoku, ATWD trails the baseline in the mean (0.248 vs. 0.269) and on two of three seeds. Per seed, the baseline solves 3 fewer, 15 more, and 37 more of the 800 puzzles than ATWD (Table 6). The comparison ATWD wins is against hard-freeze. That ablation changes both the training decay (δ_train = 0) and the refresh (R = 0), as the authors acknowledge (L. 026–028, 349–350, 472–473; App. A.10). Hard-freeze is also itself 7.1 pp below the baseline (0.198 vs. 0.269). Beating it therefore does not show that refresh or per-token damping improves on the standard solver.

The "reliability inversion" (Sec. 5.3; Fig. 1) compares cross-seed SDs from three runs per arm. A 95% interval for an SD with two degrees of freedom spans roughly 0.52× to 6.3× the point estimate, so the inversion is a descriptive observation rather than an established effect. Finally, R = 20 was chosen from a single-seed, 2-epoch A5 sweep in which aggregate accuracy varied by only 1.4 pp across R ∈ {10, 20, 30, 50} (Table 4; L. 700–712). It was then reused for S5 and Sudoku (L. 282–283, 702–703; acknowledged at L. 467–470). This matters because the paper's positive claim requires at least one benefit that is robust across seeds and attributable to ATWD rather than to baseline instability. The current evidence provides neither.

Questions for authors
  1. Can you add controls that separate per-token allocation from the refresh? These would be (a) scalar damping with the same periodic refresh (R = 20), (b) a no-decay arm (η ≡ η0), and (c) the matched-decay, no-refresh arm of App. A.10. If ATWD's A5 gain persists against (a), per-token allocation would be implicated. If (a) matches ATWD, the benefit would instead come from limiting cumulative damping.
  2. How robust is the A5 result? Please report more seeds per arm (e.g., five or more) and per-seed training curves. Were the two weak baseline seeds (0.308 and 0.058) still improving at 15 epochs? Did their scalar step-size decay heavily or reach the 10⁻³ floor during training? Does the gain persist at the originally planned budget of 2,000,000 examples and 50 epochs?
  3. Does ATWD change when sequences halt? Please report evaluation iteration counts (eval/steps) for A5 and for all Sudoku seeds, ideally with per-example rather than per-batch halting. Please also report the distribution of per-token step-sizes during training and evaluation. If ATWD has no effect on halting, what does "per-token halting" in the title refer to?
  4. On S5, what is the final training accuracy of the ATWD runs, and what is their evaluation accuracy restricted to k ≤ 32? Could token-resolved replays under the native evaluation settings show whether the collapse lies in the weights or in the solver? Cross-evaluation could help with the same question: running the ATWD-trained checkpoint with the scalar solver, and the baseline checkpoint with the ATWD solver.
  5. Which puzzle is "the initially inspected puzzle" in Sec. 6.2 (L. 420–422)? How does "80 for seed 0" relate to the Fig. 6 caption, which states that all 81 grid cells of Example 3 converge? Are "Example k" and "puzzle k" the same puzzle?
  6. What data underlie the "train/steps volatility" row of Table 7, and at which training steps do Sudoku seeds 1 and 2 reach the halting-budget cap?
  7. Are the "21.9%/20.7% fewer" violations (L. 371) computed on the failed-subset metric only? What are the violation counts on the puzzles that all three arms fail?

Minor:

  • Title and Fig. 1 caption (L. 066): "per-token (adaptive) halting" should read "token-wise damping" (see Critical Weakness 1).
  • "Equation equation" appears at L. 174, 199, 207, 652, and 694, apparently from cross-reference output combined with a literal "Equation". In Eq. 5 (L. 169–170), the indicator renders as "⊮" (the "does not force" symbol) instead of 𝟙 or an Iverson bracket.
  • L. 174–175: the central property was "verified before training (Section 4)", but the tests are in App. A.2, and Section 4 does not describe them.
  • L. 345, L. 361–362, and the Fig. 1 caption (L. 069) cite Table 2 for per-seed comparisons, but Table 2 reports only means. The per-seed values are in Table 6.
  • Fig. 1 caption (L. 068–069): ATWD is said to beat hard-freeze "by a wide margin on every seed", but the seed-1 margin is 27 of 800 puzzles (3.4 pp), and hard-freeze is not plotted in Fig. 1.
  • Table 3 (L. 339): "+21.9% vs. base" uses a plus sign for a reduction. Please also state that the "21.9%/20.7%" at L. 371 refer to the failed-subset column; the overall reductions are 14.3% and 15.3%.
  • Fig. 5 (p. 17, L. 886–888) shows 24.84/30.94, 28.96/39.61, and 29.31/39.01, whereas Table 3 reports 24.85/30.97, 28.98/39.65, and 29.33/39.04. Its x-axis label also writes "ATWD (r=20)" for R = 20.
  • Table 9 caption (L. 1010–1011): it says "Arm (4) is not run", but the arm that was not run is labeled (2) in the table (L. 1014) and in the text (L. 1004–1007).
1 comment
AuthorsOpenReview ↗

Response to Reviewer 4Uap

Thank you for the detailed review. It led to the most important changes in the revision.

W1 (title, framing). We agree. The title, abstract, introduction, Sec. 4.3, Fig. 1, and ethics text now say "token-wise damping". The paper states that ATWD does not change halting or compute (Sec. 6.3). The gap is now stated as the shared scalar step-size driven by the slowest token.

W2 (evidence for an ATWD-specific benefit). Your concern was correct. The new controls show that the A5 gain is not ATWD-specific.

  • On seed 1, sequence accuracy is 0.879 (scalar damping + refresh), 0.912 (token-wise, no refresh), and 0.895 (no damping), against ATWD 0.891 and baseline 0.308.
  • Scalar damping + refresh on seeds 0 and 2 reaches 0.994 and 0.853. The mean is 0.909±0.075, against ATWD 0.948±0.050.
  • On Sudoku, the matched-decay arm without refresh scores 0.274 on seed 0, against ATWD 0.271 and hard-freeze 0.190. So the ATWD–hard-freeze gap is attributable to the decay rate, not refresh. We rewrote the abstract and conclusion accordingly. The SD-based "reliability inversion" is now described as a descriptive observation, with your interval caveat. The R=20 choice is stated as a default.

Q1 (controls). Done as described above. Controls (b) and (c) are single runs on seed 1, which we picked because baseline and ATWD differ most there. We state that this was an outcome-informed choice. Baseline varies from 0.058 to 0.930 across seeds, so single-run differences below that range are not interpretable. The Sudoku scalar-refresh and no-damping arms and all S5 controls were not run.

Q2 (A5 robustness). We did not add seeds beyond those reported. The weak baseline seeds were still improving at epoch 15: sequence accuracy at epochs 5/10/15 was 0.000/0.034/0.308 for seed 1 and 0.003/0.008/0.058 for seed 2. We did not test a longer budget. We did not measure the baseline's step-size or floor events. train/steps cannot separate residual halting from floor halting, and the appendix says so. The originally planned 2M-example, 50-epoch budget would need about 300 GPU-hours per arm, which we could not run.

Q3 (effect on halting). Final eval/steps on A5 is at or near the 160 cap for all arms (Table 10). On Sudoku all arms reach the 1,000 cap. The first training step at which evaluation reaches the cap is:

  • ATWD: 2241/2241/2988
  • baseline: 4482/5229/4482
  • hard-freeze: 6723/7470/6723
  • matched-decay control (seed 0): 3735 Evaluation halting is batch-level. We did not measure per-example halting or step-size distributions, and we say so.

Q4 (S5).

  • Training accuracy for ATWD (mean of the last 100 logged steps) is 0.388 and 0.065.
  • Per-token accuracy at k=32 is 0.046 and 0.041 (native) / 0.042 (scalar) for ATWD, against 0.839 and 0.932 for baseline (Table 11). The failure is therefore present at the training length.
  • Evaluating the ATWD checkpoints with the scalar solver gives the same accuracy as with the ATWD solver (0.024 vs 0.024, 0.017 vs 0.017). The collapse is in the weights.
  • Baseline weights lose accuracy under the token-wise solver (0.474→0.356, 0.735→0.704).

Q5. Puzzles are indexed from 0, and "Example k" is puzzle k. The text now says "puzzle 0".

Q6. The cap-reaching steps are given under Q3. The appendix (Table 12) reports the training-step statistics with a stated, post-hoc definition, and Table 7 and Sec. 5.5 have been updated accordingly. Hard-freeze has the lowest coefficient of variation (mean 0.12 vs 0.23 baseline and 0.29 ATWD) but the highest mean absolute step-to-step change (0.55 vs 0.29 and 0.40), because its training steps stay near the cap of 12. We therefore no longer claim hard-freeze is more volatile.

Q7. On puzzles that all three arms fail (a repeat audit, Table 13), hard-freeze has fewer violations on every seed. The means across seeds are 34.13 for hard-freeze versus 40.04 for baseline and 40.11 for ATWD (14.8%/14.9% fewer; mean n=574). The repeat audit's solved counts differ from the first audit's by up to 3 of 800 puzzles, which we state. The 21.9%/20.7% figures refer to the failed-subset column. The overall reductions are 14.3%/15.3%.

Minor points. The cross-reference errors, the indicator symbol, the table and caption references, the "+21.9%" sign, Fig. 5 vs Table 3 values, and the Table 9 caption were fixed.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response and Summary of Changes

We thank the reviewers. In response, we ran the requested controls, cross-evaluations, and audits, uploaded the revised PDF and updated supplementary code, and changed the paper's claims where the data required it.

Main changes:

  1. Title and framing. The title is now "When Does Token-Wise Damping Help?" The text no longer says "per-token halting". ATWD leaves FPRM's halting rule and per-iteration compute unchanged.
  2. A5 controls. Scalar damping with the same refresh (3 seeds), token-wise damping without refresh (seed 1), and no damping (seed 1) all reach accuracy comparable to ATWD. ATWD's gain over the baseline is therefore not attributable to per-token allocation.
  3. Sudoku control. A matched-decay arm without refresh (seed 0) scores 0.274, against 0.271 for ATWD and 0.190 for hard-freeze. The ATWD–hard-freeze gap thus reflects the decay rate, not refresh.
  4. S5. Cross-evaluating checkpoints with the other solver places the collapse in the trained weights.
  5. Other additions. New appendix material covers the A5 epoch trajectories, halting-cap and training-step statistics (updating Table 7), and a repeat audit on puzzles that all arms fail.
  6. Abstract, discussion, conclusion, and limitations were rewritten to match. Minor errors and figure legibility issues were fixed.

Limitations that remain: the no-damping and token-wise-no-refresh arms are single runs, and the Sudoku control is one seed. Seed 1 was chosen for the A5 controls because baseline and ATWD differ most there. No S5 controls were run.

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

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