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Paper summary
The paper studies the optimization and architecture of small recursive reasoning models that repeatedly apply shared Transformer modules to hidden states and predict complete structured outputs. It compares HRM/TRM/URM-style models under a common data and evaluation pipeline across six algorithmic domains, including two additional domains with explicit distribution shifts: Arithmetic and Game of Life. The study examines gradient truncation, physical batch size versus gradient accumulation, parameter sharing, stabilization mechanisms, and additional model or inference-time computation. The resulting 13.6M-parameter model combines these choices into a training recipe and reports improvements on several benchmarks, particularly Arithmetic OOD. The paper's central contribution is an empirical analysis of what makes recursive computation effective and reliable.
Critical strengths
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The research question is worthwhile. Understanding which architectural and optimization choices actually contribute to recursive models is useful. A focused study of small algorithmic solvers can provide a meaningful contribution without requiring experiments on large language models, provided its conclusions are well supported.
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Several comparisons incorporate useful controls. The gradient-horizon experiment fixes the forward computation and varies the differentiated portion of the trajectory. Its observation that equal numbers of differentiated module applications can produce different outcomes is informative. The batch experiment fixes effective batch size, and the shared-module comparison attempts to control parameter count. These are sensible starting points for separating factors that change together across prior systems.
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The complete recipe gives encouraging results, and the paper reports some useful limitations. Reported results include 71.16% Arithmetic OOD accuracy, 98.41% Sudoku accuracy, and 59.50% ARC-AGI-1 pass@2. Table 3 includes three-seed results on two domains, rather than relying exclusively on single runs. The paper also acknowledges that its main comparison is between complete recipes and qualifies the interpretation of its unsuccessful joint-training experiment.
Critical weaknesses
My main concern is the reliability of the empirical conclusions. The limited scope is acceptable; however, for a paper whose primary contribution is a controlled analysis, the experiments need to distinguish the proposed explanations from plausible alternatives. At present, the results establish that a particular recipe performs well more convincingly than they establish why it works or what generally limits recursive computation. These gaps weaken the claimed scientific contribution even within the paper's intended scope.
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The physical-batch conclusion does not identify the source of the observed difference. In Figure 5, changing from physical batch 8192 to batch 2048 with four accumulation steps reduces OOD accuracy from 63.16% to 37.71%, while the reported mean gradient norm increases from 0.38 to 65.46. For an additive loss, identical parameters, samples, and per-example recurrent states, correctly weighted accumulation should closely reproduce the full-batch gradient when stochasticity and numerical effects are controlled. Recurrence alone does not invalidate this equivalence. The paper therefore needs to identify which operation changes the computation or training dynamics. Loss normalization, recurrent-state handling, stochastic regularization, and update timing are possible explanations that are not separated by the current experiment. Appendix B.1 explicitly places clipping after accumulation, so per-microbatch clipping is not an explanation supported by the manuscript. Without a controlled gradient/update comparison, this result does not establish physical batch size as an independently understood property of recursive optimization.
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The gradient-horizon finding has limited replication and an unclear separation between model selection and evaluation. Section 5.1 and Appendix D study eight settings on Arithmetic with a single seed. Table 8 explicitly selects Best OOD from 40 checkpoints using the OOD split, and Figure 4 reports these best OOD values. The manuscript does not clearly identify a separate OOD validation set and untouched test set. Although the selected configuration also reaches 71.16% at the final checkpoint, the selection procedure still matters when interpreting the comparison as evidence of generalization. Repetition across seeds and another task, together with a fixed selection protocol, is needed to establish a robust intermediate optimum. The lower ID accuracy of the longest gradient setting also leaves open whether its disadvantage reflects optimization under the chosen hyperparameters rather than a general limitation of longer gradient propagation.
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The stabilization evidence does not isolate the core mechanisms, and its checkpoint statistics need reconciliation. Table 3 adds components cumulatively, while normalization and EMA remain fixed; it does not independently establish the contribution of the state-update bound or the necessity of each component in the final recipe. Some additions reduce variance while lowering mean accuracy, so these effects should be distinguished. More concretely, Table 3 reports GoL OOD accuracy of 65.80 ± 0.13 for the final configuration, whereas Appendix E describes a seed of that configuration with final OOD mean 63.77. These cannot be statistics of the same final-checkpoint results if that run is among the three seeds. Its peak OOD score of 65.67 may be compatible with a best-checkpoint interpretation, but that protocol must be stated: consistency of peak performance is different from stability of the final trained models. This ambiguity directly affects a central claim of the paper.
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The overall gains are not sufficiently attributed to the proposed optimization choices. The main comparison changes model size, physical batch size, and the training recipe together: for example, the evaluated TRM/URM models have 7M parameters, versus 13.6M for the proposed model. Section 4.6 appropriately acknowledges this recipe-level comparison, but it cannot by itself show that optimization choices account for a large fraction of the total improvement. Applying the proposed training changes to the same backbone, alongside the corresponding unchanged-training controls, would make that attribution substantially stronger. The present local ablations do not fully bridge the gap between the overall improvements and the claimed explanation.
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The architecture and scaling conclusions exceed the comparisons reported. Section 5.3 changes whether the two recurrent transformations share weights, while retaining nested two-state updates. This tests the need for separate parameters, not the need for hierarchical recurrence as a whole. The exact configurations used to match parameter count should also be specified. Section 5.5 gives conclusions about increased depth, width, and head count without a complete sweep of settings and results. Figure 6b does not clearly specify the starting and ending inference budgets. A controlled evaluation relating task difficulty to training and inference recurrence would be much more informative about scaling limits than the current aggregate gains.
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The inference-cost reporting appears inconsistent. Figure 1 places the proposed model at 6× relative inference compute, whereas Table 7 defines its cost per complete answer as 6T relative to the dense control. With the budgets described in Appendix B.3, T is typically 16 and is 8 for ARC-AGI-1, corresponding to 96× or 48× under the paper's own layer-application accounting. The figure appears to omit this multiplier, or to use an unexplained normalization. This should be reconciled before using the figure to support efficiency comparisons. These layer counts should also be distinguished from measured FLOPs or latency.
Questions for authors
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Gradient accumulation: With fixed parameters, the same examples and recurrent states, stochastic regularization disabled, and controlled precision, do a full batch and correctly weighted microbatch accumulation produce matching losses, gradients, and one-step updates? If not, which operation introduces the difference? If they do, where do the training trajectories first diverge?
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Selection and replication: Which datasets select checkpoints and hyperparameters, and which are reserved for final testing? Can the key gradient-horizon comparison be reported under a fixed selection protocol across multiple seeds and another domain, with a small sensitivity check for the training hyperparameters?
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Stability statistics: Which seeds and checkpoints contribute to Table 3? Does it report final or peak accuracy, and how does seed 536 in Appendix E relate to those results? Please provide the per-seed values and clarify the checkpoint and recurrent-output selection rules.
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Core components and attribution: Which gains remain when the update bound, gate, and normalization are individually removed from the final recipe? Does applying the training recipe to an otherwise unchanged baseline backbone recover the main improvements? These comparisons would help distinguish component effects from the effectiveness of the complete combination.
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Architecture and scaling: What are the exact parameter-matched configurations in Figure 6a and the inference budgets in Figure 6b? Can the depth/width results be reported explicitly? Does the hierarchy conclusion survive a comparison that removes nested updates while controlling parameter count and recurrent computation, or should the claim be narrowed to weight sharing?
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Cost accounting: How is the 6× value in Figure 1 reconciled with the 6T cost per answer in Table 7? Please provide a consistent complete-answer cost definition for all plotted systems, including the autoregressive baselines.
Thank you for your detailed feedback and questions.
Why do Table 3 and Appendix E report different Game of Life scores? For Table 3, we took the maximum score across checkpoints for each seed (125, 536, and 782), then averaged these per-seed maxima. The value 63.77 in Appendix E is the score at the last checkpoint of seed 536. We have clarified in the manuscript where best-checkpoint and last-checkpoint scores are reported.
Why does Figure 1 show 6× while Table 7 gives 6T? We report compute relative to a single forward pass of the dense baseline (1×), so each value indicates how many times as much computation a model requires as the dense baseline. We have clarified in the figure caption that Figure 1 shows the minimum amount of compute guaranteed to be used for every prediction, corresponding to one ACT step. Table 7 includes the total number of ACT steps, T. The detailed accounting formula is already provided in Appendix C.2.