The paper's headline claim, that "knowledge-source arbitration is implemented through the flexible reconfiguration of a shared population rather than a dedicated conflict circuit," is not supported by the experiments. At a high level, it is unclear whether the paper is studying arbitration at all, since in both settings the model is explicitly instructed which source to use. It could be that the mechanism being interpreted is closer to instruction following.
The main confounder is that the score used to select neurons conflates two things, namely how strongly a neuron's activation changes under conflict and how strongly it writes into the communication subspace. It is not surprising or significant that ablating the most conflict-responsive neurons affects the answer more than ablating random neurons, even if the random neurons do not write into the communication subspace, so the ablation results do not show that the subspace is important. Similarly, since both instruction settings use the same references and questions, the most conflict-responsive neurons are likely to be the same under both settings, so the overlap between the two pools could come entirely from the conflict-effect term of the score rather than from the subspace. Comparing against pools selected by conflict-effect magnitude alone would address both these concerns.
Additionally, since the two pools share most of their neurons, it is unsurprising that they behave identically under ablation. The "path-dependent" effect the authors describe, i.e. that ablating either pool hurts context-following more at earlier layers and memory-following more at the last layer, could simply be because overriding the model's memory is harder than following it, since all facts are filtered so that the model's memory agrees with the ground truth. Since the shared-pool and ablation results are the paper's main evidence, without stronger controls they do not tell us anything specific about communication subspaces or knowledge conflicts.
A more faithful characterization of the results would be that some neurons activate selectively under knowledge conflicts and matter for the model's answer (i.e. ablating them shifts the model's response), which is already known from prior work. The only evidence for a communication subspace is that it predicts the later layer's conflict effects better than a random subspace does. This is purely correlational and does not meet the bar for the mechanistic claim that conflicts are resolved through a shared neuron population communicating via low-dimensional subspaces.
As a more minor (but salient) point, this paper was very difficult to follow. I had to re-read certain sections multiple times, skip ahead to other sections, and consult with an LLM in order to fully understand what was going on. For example, the key idea of a source-target MLP communication subspace was never defined, and many non-standard terms were used without context ("additive contrast assumption", "path-dependent functional pattern", "behavioral readout", "task-specific loadings", "loading-defined pools", etc...). While I listed this as a minor point, I think it actually contributes quite a bit to my recommendation. I would have no reason to doubt, a priori, the epistemic quality of the paper, but the lack of care given to the writing makes me question if the authors actually vetted their experimental results.
Thank you for identifying three issues: terms that are not defined, a risk of over-interpretation, and no causal evidence for the described geometry. We accept all three. We will add a consolidated definitions table and have already narrowed the exclusivity claim and tested the geometry directly. Your third point in particular moved us from description to intervention.
1. Definitions (W1, Reviewer Q1)
These terms already have scattered definitions in §3.2 and Appendix A.1, in the revision we will add a consolidated 11-term table in Appendix A.1 for easier reference. Here are the three you named.
The two-task eligibility test requires both tasks to exceed the 95th percentile of R²/cosine against 50 random source bases, and the 95th percentile of coordinate correlation against 50 paired shuffles.
The validation rule keeps, for each source layer, the target layer with the highest mean Validation R² across both tasks, no Test causal result is used.
Validation write energy is the squared norm of the centered Validation shared write. The reconstruction rate is the fraction captured by the basis. The remaining terms (conflict effect, U, communication load, loading-defined pool, shared/context-only/memory-only, reconstruction drop, w/τ/s, path-dependent) will go into the same table; non-standard usages such as path-dependent will get a one-sentence definition.
2. Shared overlap, non-shared members, and attention (W2, Reviewer Q2)
Sharing 65–68% of each pool does not mean there is no specialization. We took the exact difference sets of the two Top-512 pools and ablated them under both tasks, against same-layer, same-size random pools.
Table 1 | Difference-set ablations. L19, 109 Test facts; s = own-task τ − other-task τ; shared-core context τ is shown for reference.
Non-shared members do carry weak but reliable selectivity, far smaller than shared-core, at L20 the values are +0.142 / +0.288, and by L24 they approach zero. The accurate statement is therefore "shared population first, weak specialization alongside," and we no longer make the claim that no dedicated components exist.
You also noted that we examined only MLP neurons. We added a head screen across all 32 layers and an L19 ablation: top-8 heads overlap 6.84/8 on average between tasks (minimum 4/8), and top-16 overlap 14.56/16 (minimum 12/16); at L19 the top-8 sets are identical, and top-16 overlap 13/16. Ablating either set hurts the context task more (context-top16 1.374, memory-top16 3.243), with no task-specific dissociation; generation switches are 3.7% and 11.6%, against 0.3% for random. We therefore find no evidence for dedicated heads.
3. Causal role of the geometry (W3)
You say the paper does not show that the described geometry has causal effect. We agree: the discussion already states that we do not establish that the geometry itself causes the intervention effects, if the framing suggested a causal claim, we will clarify it in the revision. To answer directly, we removed G by projection and by a norm-preserving swap, and we removed the 16-dimensional U.
Table 2 | Causal checks for G and U. Test 109, Validation 70, 3 templates each; swap = mirror reflection across the two task bases (norm preserved); τ>0 = stronger weakening than random.
G is weak on Test and does not replicate on Validation. Under swap it is asymmetric, and it is no better than a random projection at predicting choice. It flips no answers. G is therefore an organization pattern, not a task-specific causal mechanism. Removing the 16-dimensional U, by contrast, has a strong context-specific effect. Details of the direct interventions are in our response to ci2m (Sections 1–2). We will stop calling the geometry a causal mechanism and keep only the shared population and its task-related organization, the functional role of U is reported separately.