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Paper summary
The paper asks whether the “latent recursion” effect, where re-executing a contiguous block of layers in a frozen LLM fixes wrong answers, survives a full post-training pipeline. The authors enumerate a closed family of L(L+1)/2+1 routes, each repeating one block once, on every instance. From this they define a recursion budget B (the fraction of instances the default pass gets wrong but some route gets right, equal to the instance-oracle gap), a fix density ρ_fix, and transitions between “always-correct”, “in-budget” and “out-of-reach” categories across checkpoints. Across 21 checkpoints from 8 MLLM families, B is large, while the best fixed route gains at most +2.7 and transfers poorly across split halves. Along released Qwen3 → InternVL3.5 intermediate checkpoints, B and ρ_fix generally fall, most sharply at instruction tuning and multimodal adaptation. RL stages never turn an out-of-reach instance into an always-correct one, whereas SFT stages do. For newly learned instances, weight-update norms, logit-lens shifts and hidden-state shifts from post-training align with those of the best recursion route at the earlier checkpoint, more than for a control set. Three test-time methods (POLAR, Dr.LLM, TFLT) give no gain on InternVL3.5-2B. As an alternative, the paper proposes recursion-aware GSPO, which trains through a fixed per-category route chosen on a 2k-instance subset. This method beats standard GSPO in 5 of 6 categories on InternVL3.5-2B and in 14 of 18 cells across three more backbones, supported by compute, route-choice and cross-category ablations.
Critical strengths
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Enumerating a closed route family instead of searching or sampling makes B, ρ_fix and the transition matrices exactly comparable across checkpoints. This avoids the search noise that limits prior work and gives a well-defined upper bound for any route selector.
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The matched-cardinality comparisons (temperature sampling, Monte-Carlo routes), split-half transfer, and reproductions of three routers from official code are informative. The finding that test-time routing fails on fully post-trained MLLMs is useful.
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Recursion-aware GSPO adds no parameters at 1.06–1.23× step time. It wins in most backbone–category cells over three seeds, and the inference-only, two-epoch, and random-route ablations suggest the gain comes from route placement rather than extra compute.
Critical weaknesses
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The out-of-reach sets are only 0.7–4.7% of small benchmarks and are pooled across scales, so a zero count may reflect a few dozen instances. The result is also expected under the generic sharpening view and does not specifically implicate recursion.
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Both the target set and the “best route” are selected to move toward the correct answer, so high logit-space cosine is nearly guaranteed by construction. A random-correct-route or sampling-based null is missing, the control set’s best route is undefined, and the representation and weight-space signals are small or inconsistent across scales.
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Section 3 argues that useful routes are instance-specific and that fixed routes don’t transfer, yet the method trains through a fixed per-category route chosen on a few hundred instances. That selection is noisy (Top-2 underperforms GSPO; a random route costs −7.56), and the claimed “re-entry-stable representation” mechanism is never measured.
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Dr.LLM collapsing to ~20% while never choosing the default route suggests an adaptation failure rather than low ρ_fix. The routers are never tested on earlier MLLM checkpoints, so the causal claim that post-training causes routing to fail is untested.
Questions for authors
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Please give absolute instance counts, per scale, for the out-of-reach → always-correct cells under RL and SFT, plus a significance estimate. How large is the out-of-reach set per checkpoint before pooling?
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For section 5, what is the cosine similarity between Δf and the shift of a random correct route, or of a correct temperature sample, on the target set? How exactly is the “best recursion route” defined for control-set instances?
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Do POLAR/Dr.LLM/TFLT recover gains on earlier InternVL3.5 checkpoints (Pretrained/Instruct) in your multimodal adaptation? Without this, the failure on the final checkpoint cannot be attributed to post-training rather than to the adaptation.
4 comments
Part 2/2: Response to Reviewer LGdC
W3: Section 3 argues that useful routes are instance-specific and that fixed routes don’t transfer, yet the method trains through a fixed per-category route chosen on a few hundred instances. That selection is noisy (Top-2 underperforms GSPO; a random route costs −7.56), and the claimed “re-entry-stable representation” mechanism is never measured.
We agree that a fixed route cannot recover an instance-specific budget, and we no longer describe the method that way. However, Sec. 3 and Sec. 6 test different things. Sec. 3 applies a fixed route to frozen weights at test time, while Sec. 6 trains through the route so the weights adapt to it. The two results are consistent. Applied at test time without training, the selected route stays below the baseline in five of six categories (Table 2, Rec. Baseline), as Sec. 3 predicts. Trained through, the same route beats standard GSPO in five of six categories. The method therefore uses the route as an inductive bias during training rather than applying it to frozen weights.
Route sensitivity. We agree that the ranking below the top-1 is noisy. The original random route r6,12 is seven layers long, while the top-1 route is one layer. Repeating a random long block can be disruptive, since few routes are useful (Fig. 14) and post-trained layers have more distinct roles (Fig. 9). We therefore add random routes matched in length to the top-1 route.
Table R3. STEM route choice with length-matched random routes (InternVL3.5-2B)
| Route | Layers | Change vs standard GSPO |
|---|---|---|
| Top-1, r19,19 | 1 | +1.88 |
| Top-2, r1,1 | 1 | −0.30 |
| Top-3, r10,14 | 5 | +0.58 |
| Random, r6,12 | 7 | −7.56 |
| Random single layer, r26,26 (new) | 1 | +0.48 |
| Random single layer, r7,7 (new) | 1 | +0.14 |
Most of the −7.56 loss comes from the random route's length. Random single-layer routes stay close to standard GSPO (+0.48 and +0.14). At matched length, the top-1 route beats them by 1.4 to 1.7 points, so the top of the depth map carries real information about where to loop. The top-2 route was chosen from only 333 STEM instances, and we expect a larger selection set to make the ranking below the top-1 more reliable.
Re-entry mechanism. We measured how similar the first-pass and second-pass outputs of the repeated block are, using linear CKA as in Appendix C.2. Recursion-aware GSPO raises this similarity from 0.728 to 0.749. With the same route applied, standard GSPO lowers it to 0.710. The two trainings move it in opposite directions, which supports the re-entry mechanism.
W4: Dr.LLM collapsing to ~20% while never choosing the default route suggests an adaptation failure rather than low ρ_fix. The routers are never tested on earlier MLLM checkpoints, so the causal claim that post-training causes routing to fail is untested.
Table R4. Test-time routing along the checkpoints (ARC-Challenge)
| Checkpoint | Stage | Fix density | TFLT gain | Dr.LLM gain | POLAR gain |
|---|---|---|---|---|---|
| Qwen3-1.7B-Base | LLM Pretrain | 0.321 | +1.8 | +2.5 | +0.1 |
| Qwen3-1.7B | LLM Instruct | 0.149 | +0.6 | −0.5 | −0.4 |
| InternVL3.5-2B-Pretrained | MLLM Pretrain | 0.114 | −0.1 | −0.3 | −0.2 |
| InternVL3.5-2B | MLLM GSPO | 0.087 | −0.3 | −1.2 | −0.6 |
We agree that Table 1 alone does not test this link. Table R4 runs the three test-time methods on earlier checkpoints of the same family. We use ARC-Challenge, where fix density is known for every stage.
The methods work before post-training and stop working after it. On Qwen3-1.7B-Base, TFLT and Dr.LLM gain +1.8 and +2.5 points, or +1.5 on average across all three methods. After LLM post-training, no method gains more than +0.6. On the final model, all three fall below the default route (−0.3 to −1.2). The average gain falls at every stage, tracking the fall in fix density from 0.321 to 0.087. We have added this table to Sec. 6.
Reference
[1] Yue, Yang, et al. "Does reinforcement learning really incentivize reasoning capacity in llms beyond the base model?." Advances in Neural Information Processing Systems 38 (2026): 57654-57689.
[2] Matsutani, Kohsei, et al. "Rl squeezes, sft expands: A comparative study of reasoning llms." International Conference on Learning Representations. Vol. 2026. 2026.
[3] Yang, An, et al. "Qwen3 technical report." arXiv preprint arXiv:2505.09388 (2025).
Response to authors
I thank the authors for the detailed response and the new experiments. W2 and W3 are partly resolved. My remaining concerns are below.
W2: I appreciate the nulls in Table R2, but they confirm my concern rather than resolve it. Within the target set, the best recursion route (0.66) cannot be told apart from a random correct route (0.59), and best-of-N (0.75) aligns more. So the logit alignment mostly reflects correction toward the right answer, not anything specific to recursion.
The two remaining signals are weak:
With answer options removed, 0.14 ± 0.03 overlaps with 0.11 ± 0.04 (best-of-N) and 0.09 ± 0.03 (random correct). The hidden-state value is 0.04 ± 0.02, against −0.01 ± 0.02 for a random correct route. The response says the pattern holds at 1B to 8B, but no numbers are shown.
The target-vs-control comparison in Fig. 5 is not a matched contrast either: control instances are already correct, so there is no correction direction for them to align with.
The revised abstract now says the alignment holds “beyond what shared error correction explains”. Table R2 does not support that. Sec. 5 and the conclusion also still say the alignment “confirms” absorption and is “not coincidental”.
W3: The distinction between train-through and test-time use is convincing, and the length-matched random routes show that most of the −7.56 came from route length. However, only top-1 stands out. Top-2 does worse than both random single-layer routes. With two random draws in one category and no seed variance, this supports “the top-1 route is good in STEM”, not “the utility map ranks routes reliably”.
Response to Reviewer LGdC
We thank the reviewer for the careful follow-up. We respond to the remaining points below.
W2. Alignment beyond shared error correction.
We agree that the logit alignment in Table R2 largely reflects shared error correction, and the revised Section 5 states this. However, the 2B MPO → GSPO hidden-state result (0.04 / −0.01) comes from one of the weakest settings. To show this, we extended the hidden-state analysis with the same nulls to all four scales and three transitions.
Table R5. Hidden-state alignment, mean over layers 21 to 27 (best recursion route / random correct route)
| Scale | Pretrain → Instruct | Instruct → MPO | MPO → GSPO |
|---|---|---|---|
| 1B | 0.15 / 0.13 | 0.04 / 0.01 | 0.07 / 0.03 |
| 2B | 0.11 / 0.10 | −0.01 / −0.01 | 0.04 / −0.01 |
| 4B | 0.23 / 0.05 | 0.12 / 0.01 | 0.24 / −0.01 |
| 8B | 0.31 / 0.22 | 0.10 / 0.02 | 0.16 / 0.03 |
At 4B and 8B, the best route reaches 0.10 to 0.31 and stays above the random correct route in all six panels, for example 0.24 against −0.01 at 4B MPO → GSPO. The random correct route fixes the same instance at the same checkpoint, so shared error correction alone would predict the same alignment. The gap therefore points to shared structure beyond correction. Best-of-N has no hidden-state counterpart, since sampling does not change the forward pass. The same separation appears in logits with option tokens removed (about 0.6 against 0.1 to 0.2 at 4B MPO → GSPO). The full curves are in the revised Appendix D.2 (Figs. 12 to 14).
We agree that target versus control is not a matched contrast. Fig. 1 and Fig. 5 now compare the best route with a random correct route and a shuffled route on the same target instances. We also updated the abstract and introduction accordingly.
W3. Reliability of route selection.
We agree that the ablation alone supports "the top-1 route is good in STEM". The STEM ranking in the paper is based on only 333 instances, which is the STEM share of the 2k selection subset. To test how stable this ranking is, we repeat the selection with larger STEM sets in Table R6.
Table R6. STEM route ranking by selection-set size (InternVL3.5-2B)
| Instances | Top-1 | Top-2 | Top-3 | Top-10 overlap with N = 2000 |
|---|---|---|---|---|
| 333 | r19,19 | r1,1 | r10,14 | 0.5 |
| 500 | r19,19 | r10,14 | r26,26 | 0.7 |
| 1000 | r19,19 | r10,14 | r16,19 | 0.9 |
| 1500 | r19,19 | r10,14 | r16,19 | 1 |
| 2000 | r19,19 | r10,14 | r16,19 | 1 (reference) |
The top-1 route is r19,19 at every size. The rest of the ranking converges as the set grows. From 1000 instances on, the top 3 is identical, and the top-10 overlap with the 2,000-instance ranking reaches 1 at 1,500. The second-ranked route at 333 instances, r1,1, drops out of the top 5 from 500 instances on. Its weak training result (−0.30 against standard GSPO) therefore reflects noise from the small selection set rather than the ranking itself.
Once the ranking is stable, the second-ranked route is r10,14. In our ablation this route was ranked third and already improved over standard GSPO (+0.58). So both of the top two routes in the stable ranking improve over standard GSPO, and the top-1 route gives the largest gain (+1.88).
We thank the reviewer again and hope the extended results and the narrower claims address the remaining concerns.
Part 1/2: Response to Reviewer LGdC
We thank the reviewer for a careful review, and for finding the measurement, the router reproductions, and the training method useful. We address each question below.
Table R1. Out-of-reach instances and their flow to always-correct (pooled over scales)
Table R1 gives the counts for every transition on both benchmarks. Each RL transition starts from 108 to 271 out-of-reach instances. For a zero count out of n, the table reports the exact one-sided 95% upper bound. On MMStar, the SFT rates are far above the RL bounds: 12.0% vs. 1.1% for InternVL3.5, and 8.7% vs. 2.1% for InternVL3.
We agree that the zero flow under RL is what the sharpening view predicts [1,2]. The link itself is our own finding, though. Recursion and best-of-N sampling reach largely the same instances (Jaccard 0.86 to 0.97, Table R2 in our reply to r217), so the recursion budget is the same headroom that sharpening consumes. What is specific to recursion is location in depth. For each instance and task, recursion shows which depth band carries the headroom, which sampling cannot (Figs. 14 and 15).
Table R2. Alignment between the post-training shift and each intervention. InternVL3.5-2B, MPO → GSPO, MMStar, mean over layers 21 to 27, mean ± standard error.
For both sets, the best recursion route is the correct non-default route with the highest average log-likelihood of the ground-truth answer tokens. Table R2 tests the alignment against the two nulls the reviewer suggested, plus two more:
The target-versus-control gap does not come from the route choice. With routes matched in length and position, control alignment drops further, to −0.17. The alignment also requires the route to fix the instance, since shuffled routes show none (−0.05). A random correct route gives 0.59, and best-of-N sampling gives 0.75, more than the best recursion route (0.66). The higher value for sampling is expected, since RL directly reinforces correct sampled rollouts. Most of the logit alignment therefore reflects shared correction on the budget that recursion and sampling share (Reviewer r217 Table R2).
We also tested logit alignment without answer options so it becomes free-form answer now. The best recursion route on Target is 0.14, the highest value in the table and clearly above both control rows (0.07 and 0.01). As the reviewer noted, the hidden-state alignment is small but what matter here is the relative difference. Target with best recursion route outperform all null settings (0.04 vs. -0.03 & -0.05) and this pattern prevails across all pattern we tested (1B,2B,4B, and 8B). We will update Sec 5. according to this results.