acceptodds
Under review as a conference paper at ICLR 2027

Train on the Syndrome Stream You Will Decode

Abstract

Quantum error correction (QEC) turns repeated syndrome measurements into correction decisions. Neural decoders have gained widespread attention because they can learn complex, hardware-specific noise correlations directly from data. Neural decoders are usually trained and judged on reset-bounded memory experiments, assuming that benchmark winners remain best during uninterrupted computation. However, we find that this ranking can reverse. On never-reset surface-code streams at , convolutional checkpoints that beat correlated matching by 12-17% on memory benchmarks fall behind it by on interior decisions, while released graph and transformer decoders show the same failure. To identify the source of this reversal, we use controlled interventions, which trace it to preparation and terminal-readout boundaries rather than sequence length. Building on this diagnosis, we fine-tune on interior-window labels. This restores the neural lead across all three families and, with one-window lookahead, reduces convolutional per-commit error by 40-45% versus matching in simulation. The same lesson holds for lattice surgery: a better frame predictor need not yield a better conditional parity, whereas joint frame–readout supervision improves the combined decision, and the jointly trained system lowers conditional parity error by 9-15% versus joint matching. Together, these findings make existing neural decoders stream-ready with a single fine-tuning stage and pave the way for neural decoding in fault-tolerant quantum computation.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
quantum error correction, surface code, neural decoder, distribution shift, real-time decoding

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 2 reviews, above 68% of the others.
Reviewer_uZ6uOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper asks whether neural decoders trained on reset-bounded quantum memory experiments retain their advantage when used for interior-window decisions in a continuous syndrome stream. Using fixed-representative parity increments as targets and a common syndrome cutoff, the authors show ranking reversals relative to correlated matching and recovery through interior-window training. They also study frame-readout composition in lattice surgery. The results show that improvements in individual components do not necessarily improve conditional parity after composition, and that joint supervision can improve the composed decision. The evaluation includes simulated streams, controlled training interventions, and experiments on device records.

Critical strengths
  1. Distinguishing reset-bounded memory decoding from interior-window decisions helps assess claims about deployment. Table 1 reports relative reductions of approximately 40% to 45% in buffered per-commit error compared with correlated matching using the same lookahead. Controls for continued memory training, history length, and boundaries, together with checks of the matching implementation, make these gains more convincing for the task studied.

  2. The frame-readout experiments show that reducing component error does not necessarily improve conditional parity after composition. The matched comparison of joint and separate supervision at d=5, B=1d = 5,\ B = 1 supports training and evaluating the composed target directly. This provides useful evidence for assessing modular decoding systems, where component rankings alone may be misleading.

Critical weaknesses
  1. The abstract should define more precisely what it means to make existing decoders "stream-ready." The reported gains concern local and conditional targets. Their implications for complete correction with an estimated incoming frame remain untested. Section 4.3 evaluates the block contribution J=mraw⊕q0J = m_{\mathrm{raw}} \oplus q_0, where q0q_0 is the reference parity of the noisy state at the start of the block. As the authors explicitly note, complete correction relative to an ideal input reference also requires the incoming frame:

    C0=q0⊕q⋆,E=J⊕C0.C_0 = q_0 \oplus q_{\star}, \qquad E = J \oplus C_0.

    The current surgery experiment does not directly test composition with an estimated incoming frame. For eJ=J^⊕Je_J = \hat J \oplus J and eC=C^0⊕C0e_C = \hat C_0 \oplus C_0, the complete error probability satisfies

    Pr⁡(E^≠E)=Pr⁡(eJ=1)+Pr⁡(eC=1)−2Pr⁡(eJ=1,eC=1).\Pr(\hat E \ne E) = \Pr(e_J = 1) + \Pr(e_C = 1) - 2\Pr(e_J = 1, e_C = 1).

    A lower error rate for JJ alone therefore does not determine decoder rankings for the complete operation. The paper itself reports a reversal after composition, which gives a concrete reason to examine this issue. Figure 15 and the device-data experiments provide complementary evidence, but do not directly answer this question for surgery with an estimated incoming frame.

    This is a limitation of the operational interpretation, not an objection to the conditional target or an allegation of label leakage. Conditional block correction can be useful in its own right, but the paper should state more clearly which conclusions about continuous operation its results support. A comparison confined to the existing surgery circuit, using an estimated incoming frame, or a convincing argument for the significance of the explicitly limited conditional task could materially change my assessment.

  2. Claims about the role of boundaries should stay within what the controls establish. Moving from memory experiments to interior-window prediction changes preparation conditions, access to final readout, and supervision. Failure of the original weights therefore shows a transfer difficulty between tasks; it does not invalidate their original memory performance, which Table 1 confirms.

    The boundary controls provide more information than a simple fine-tuning comparison. In Appendix B.2, the shorter-sequence control reduces the nominal input length from 4T4T to 3T3T while keeping the full 2T2T predecessor history accessible to the target window. Figure 3(a) calls this condition "Shorter history," but readers must consult Appendix B.2 to see that the accessible predecessor history is unchanged. The caption should make this distinction explicit. This control does not rule out effective-context-length explanations in general, and its implications should be distinguished from those of the separate history-length experiments.

    Preparation/readout interventions also change the detector-label pair. These are valid interventions on the overall boundary treatment, but, as Appendix B.2 acknowledges, they do not isolate the effects of input statistics, label semantics, and effective context.

    Please specify which alternative explanations each control rules out and qualify the abstract's attribution to preparation and terminal-readout boundaries "rather than sequence length" accordingly. The conclusion should distinguish nominal input length from accessible predecessor history. It should also distinguish the overall effect of a boundary treatment from the separate contributions of the resulting detector and label distributions. Since the central diagnosis motivates the proposed training procedure, I am asking for its scope to be made explicit, without requiring an exhaustive decomposition of these mechanisms.

Questions for authors
  1. Which conclusions about the complete operation are supported by the conditional target evaluated here? Have you evaluated E^=J^⊕C^0\hat E = \hat J \oplus \hat C_0, with C^0\hat C_0 estimated from a noisy prefix, and compared against matching under the same syndrome cutoff? If available, a limited evaluation within the existing surgery setup would directly address my first concern. I am not asking for a complete multi-gate algorithm.

  2. Which alternative explanations are ruled out by the nominal-input-length control in Figure 3(a), the history-length study in Figure 3(b), and the preparation/readout interventions, respectively? How should the abstract's attribution to boundaries "rather than sequence length" be qualified in light of these controls?

5 comments

Dear Reviewer uZ6u,

As the discussion period is nearing its end, we want to check that our responses have addressed your concerns.

Our central finding is that decoder rankings on memory benchmarks reverse on continuous streams. The cause is the boundaries inside the scored window. Training on interior windows restores the lead, both as fine-tuning and from scratch. Neural decoders today are mostly benchmarked on memory experiments. Our results provide a basis for evaluating and training them on the continuous streams that fault-tolerant computation runs on.

We have since scored the complete correction at p=0.003p=0.003, below threshold. We used the same recipe as in Table R1.

settingmatchingourschange
d=5d=5, 18 windows before the merge0.08640.0815−5.7 %
d=7d=7, 34 windows before the merge0.04840.0454−6.0 %
d=7d=7, 42 windows before the merge0.05880.0545−7.3 %

If you have further questions, please let us know.

Thank you for your time and effort in reviewing our paper!

Thank you for the detailed response. The complete-correction results and the split between readout inputs and labels address my main concerns. I also agree that the available public data do not permit validation on a continuous hardware record. I’m raising my score to 3.

Please address the following in the final version.

  1. The revised PDF is missing both the Limitations paragraph described in your general response and the complete-correction results at p = 0.003 from your follow-up. Please add both, along with the d = 9 complete-correction result once available. Include shot counts and confidence intervals for the complete-correction results.

  2. At p = 0.003, the memory-trained entries in Table 12 and all neural conditions in Figure 10(d–f) are each based on a single training run. Please report how much the results vary across independent runs.

  3. On interior commits, the device results are roughly on par with matching and slightly worse at d = 5 with 30 rounds (Table 4). The whole-run comparison in Table 17 uses the memory-benchmark metric that the paper argues against. Please avoid citing that comparison as evidence for stream decoding.

  4. In the abstract, please specify that the 40–45% figure is a per-commit result and report the complete-correction gains of 1.7–7.3% separately.

  5. My understanding is that the circuit-level depolarizing noise used throughout is the standard uniform noise model. Please include results under an additional noise model, such as SI1000. SI1000 more closely reflects superconducting hardware and gives measurement errors much greater weight, which matters because your diagnosis focuses on the terminal readout layer.

Thank you sincerely for raising your score and for reading our responses and revised PDF so carefully. Your feedback directly shaped the paper. Both the complete-correction evaluation with an estimated incoming frame and the split of the readout boundary came from your questions, and they made our claims much stronger.

The d=9d=9 run we promised has now finished. At p=0.007p=0.007, our complete-correction error is 0.399 compared to 0.406 for matching.

In the final version, we will include this result, the p=0.003p=0.003 numbers and the Limitations paragraph, with shot counts and confidence intervals for every complete-correction result. We will also report the spread across independent training runs and the SI1000 noise tests for our readout-layer diagnosis, alongside the requested edits to the abstract and the device-result descriptions.

Thank you again for your time and thoughtful review.

Reviewer_LhB4OpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
1
Soundness
2
Read review
Paper summary

This paper investigates the performance gap between neural decoders trained on conventional surface-code memory experiments and those evaluated on continuous syndrome streams. The authors demonstrate that neural decoders outperforming correlated matching on memory benchmarks can perform substantially worse on continuous streams. To address this issue, they propose fine-tuning existing neural decoders on interior-window syndrome data. The approach improves decoding performance across convolutional, graph, and transformer architectures. The paper also investigates joint frame–readout training for lattice surgery, showing improved conditional parity decoding performance.

Critical strengths
  • The paper identifies an interesting performance reversal between conventional memory benchmarks and continuous-stream decoding. The experimental analysis provides useful insights into the effects of preparation and readout boundaries.

  • The proposed approach is simple yet effective, achieving consistent improvements across different neural decoder architectures without requiring architectural modifications.

Critical weaknesses
  • The methodological novelty is somewhat limited, as the proposed approach mainly consists of fine-tuning existing neural decoders on a different training distribution and supervision target. The contribution of fine-tuning itself needs further clarification.

  • The necessity of training on fully continuous syndrome streams is unclear. In Figure 3, training with an independent-sample seam achieves comparable or even lower mean error than training on continuous streams at some distances. This raises questions about which aspects of continuous-stream training are actually essential.

Questions for authors
  • How does the proposed fine-tuning approach compare with training the same neural decoder from scratch on interior-window samples under a comparable training budget? Is memory pretraining necessary to achieve the reported improvements?

  • In Figure 3, the independent-sample seam achieves better mean performance than continuous-stream training at d = 7 and 9. If partially breaking the continuity of training history does not degrade performance, is training on fully continuous syndrome streams really necessary? What additional benefit does continuous training provide?

  • The authors attribute the performance reversal primarily to preparation and readout boundaries. However, changing these boundaries can also affect the input statistics and supervision targets. Is it possible to further distinguish these effects?

I would be willing to increase my score if these concerns are sufficiently addressed.

3 comments

Dear Reviewer LhB4,

As the discussion period is nearing its end, we want to check that our responses have addressed your concerns.

Our central finding is that decoder rankings on memory benchmarks reverse on continuous streams. The cause is the boundaries inside the scored window. Training on interior windows restores the lead, both as fine-tuning and from scratch. Neural decoders today are mostly benchmarked on memory experiments. Our results provide a basis for evaluating and training them on the continuous streams that fault-tolerant computation runs on.

If you have further questions, please let us know.

Thank you for your time and effort in reviewing our paper!

Reviewer_LhB4OpenReview ↗

Response to Authors

Thank you for the detailed rebuttal and additional experiments. The responses clarify my concerns and strengthen the empirical analysis of the boundary effects. However, while I acknowledge the practical relevance of identifying and addressing this issue in QEC, the main contribution appears to be an analysis of a QEC-specific problem rather than a substantial advancement in machine learning methodology. Given the limited methodological novelty and the lack of significant changes to the ML framework, I am not fully convinced that the contribution meets the expectations of a top-tier machine learning conference such as ICLR. Therefore, I will maintain my original rating.

AuthorsOpenReview ↗

The machine learning side of our contribution

Thank you for your reply and for acknowledging the practical relevance of this work for QEC.

We would like to explain the machine learning side of the contribution. Neural decoders are now among the most accurate decoders on memory benchmarks [1, 2], and the field compares them on these benchmarks. We show that this comparison can give the wrong ranking once the decoders run on a continuous stream. From the perspective of machine learning, this is a gap between the data a learned model is trained and evaluated on and the data it meets in use. We trace the cause to the boundaries inside the training windows, and we show that training on the decision the deployment consumes restores the lead for all three decoder families. We keep this method simple so that it can directly fix existing checkpoints. In lattice surgery, the question becomes which target to supervise. A better frame predictor need not give a better combined decision, while training on the combined decision improves it.

We hope this work contributes to machine learning for the physical sciences through QEC. In practice, our results give a way to train and evaluate neural decoders for continuous streams. In the longer term, the same principle could guide the training of learned decoders for other codes and logical operations.

If this clarifies the contribution, we would be grateful if you would reconsider your rating. Thank you again for your time and engagement.

References

[1] Bausch et al. Learning high-accuracy error decoding for quantum processors. Nature 635, 834–840 (2024).

[2] Senior et al. A scalable and real-time neural decoder for topological quantum codes. arXiv:2512.07737 (2025).

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response

For brevity we refer to Reviewers ZF4W, LhB4 and uZ6u as R1, R2 and R3.

We thank all reviewers for their careful and constructive reviews. We are encouraged that they find the gap between memory-benchmark performance and continuous-stream decoding "an important discrepancy" (R1) and "an interesting performance reversal" (R2), that R2 finds the approach "simple yet effective … without requiring architectural modifications", and that R3 finds the controls and the matching checks "make these gains more convincing" and the frame-readout result "useful evidence for assessing modular decoding systems". Each reviewer raised one decisive question, and we answered each with new measurements. The revised manuscript incorporates every experiment they asked for.


Core contributions of our work

  1. Memory-benchmark rankings reverse on continuous streams. Under a common syndrome cutoff on never-reset surface-code streams at d=5,7,9d=5,7,9, convolutional decoders that beat correlated matching by 12–17 % on memory experiments fall behind it by 1.5–1.7× on interior commits, and released graph and transformer decoders fail the same way.

  2. The cause is the boundaries inside the scored window, and the fix is to train on the decision the deployment consumes. Controlled interventions rule out nominal input length and stream continuity beyond one window, while a preparation or a final readout inside the scored window raises the error. Training on interior windows restores the lead for all three decoder families and, with one-window lookahead, reduces per-commit error by 40–45 % against matching, from memory-trained weights at about 4 % additional samples or from scratch.

  3. Component accuracy need not survive composition, and supervising the composed target fixes it. For lattice surgery, joint frame-readout supervision lowers the error of the block's conditional parity contribution JJ by 9–15 % against joint matching, despite higher component errors.


Updates of experimental results during rebuttal

  • Appendix F.2 (R3). The complete correction with an estimated incoming frame. It is below matching at d=5d=5 and d=7d=7, and the incoming frame alone is below both committed and offline matching in 11 of 12 configurations.
  • Appendix D.4 (R1). Time-varying noise. With no retraining, the decoder stays below matching at d=5,7,9d=5,7,9 under both a ramp and a burst in the physical error rate.
  • Appendix B.2 and Section 3.3 (R2, R3). From-scratch training at an equal budget, showing that the gain comes from the training windows rather than from memory pretraining, and the readout boundary split into its input and its label, showing that most of the penalty comes from a terminal detector layer absent from the stream.
  • Appendix G.1 (R1). An end-to-end latency timeline separating throughput, lookahead, response and feedforward.

Updates of in-depth discussions during rebuttal

  • Abstract and Conclusion (R3, R2). We replaced "stream-ready" with a statement of the decisions we actually evaluate, and the attribution now reads "to the boundaries inside the training window rather than to nominal input length".
  • Section 3 (R2). The section now opens with a comparison of the two tasks and defines each term at first use.
  • Appendix B.2 and Figure 3 (R3, R2). A new table states what each control changes, what it shows, and which explanation it rules out. We relabelled the control "Shorter input (3T)", with the accessible history unchanged at 2T.
  • Sections 4.1 and 4.3 (R3). Section 4.1 now distinguishes nominal input length from accessible history. Section 4.3 scores the conditional parity contribution JJ, and Appendix F.2 scores the complete outcome EE.
  • Section 4.4 and Appendix E (R1). On hardware we pretrain the decoder in simulation and adapt it with the run's recorded readout as its only label.
  • Sections 4.1 and 5, and Appendix C (R1). The self-coordinated decoder is a strong baseline and the closest system to ours. Its code and weights are not public, so the comparison uses our implementation of its training procedure, now named as such.
  • Limitations (R1). We name validation on a continuous hardware record as the main open step. Every public surface-code release we are aware of is a memory experiment.

All revisions are highlighted in red for ease of reference.

We would be glad to answer any further questions, and we look forward to the reviewers' favourable consideration of our work.

Dear Reviewer ZF4W,

As the discussion period is nearing its end, we want to check that our responses have addressed your concerns.

Our central finding is that decoder rankings on memory benchmarks reverse on continuous streams. The cause is the boundaries inside the scored window. Training on interior windows restores the lead, both as fine-tuning and from scratch. Neural decoders today are mostly benchmarked on memory experiments. Our results provide a basis for evaluating and training them on the continuous streams that a deployed decoder will face.

If you have further questions, please let us know.

Thank you for your time and effort in reviewing our paper!

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

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