- Rating
- 3
- Confidence
- 2
- Informativeness
- 3
- Presentation
- 2
- Soundness
- 2
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Paper summary
The paper examines what attention-based visual-head discovery scores select (Section 3.1). It crosses query type, attention source, and discovery corpus in a 2 x 3 x 2 design on Qwen3-VL-8B, then distinguishes steerability (CERS, Eq. 3) from necessity (NCS, Section 3.3 and Figure 8). Changing attention source or query changes the top-100 heads substantially more than changing corpus, relative to a strong split-half stability ceiling (Tables 1 and 20). Query-span discoveries show stronger necessity, whereas none of the 12 discovered sets achieves significant steering superiority under the layer-matched random-set rank test at the default strength (Table 3; p >= 0.14). Validation includes attention-matched controls, masking-location and head-count analyses, a separately audited region-contrast grid, and additional models and benchmarks (Tables 9, 13, 14, 16, 19, and 24). Section 6 turns these findings into reporting recommendations.
Critical strengths
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The controlled discovery comparison makes an otherwise ambiguous methodological choice consequential. The crossed design separates attention source, query, and corpus instead of attributing differences between two native discovery pipelines to a single factor (Sections 3.1 and 5.1). Median overlaps of 49/100 for source changes and 55/100 for query changes, versus 84/100 for corpus changes and 96-99/100 within-setting split halves, show that these are not merely sampling fluctuations (Tables 1 and 20; Appendix B.1). The row-restricted masking analysis further links the query-span sets' necessity to question/option processing rather than the final prediction row (Table 5). This is useful evidence that discovery specifications must accompany functional interpretations, not just implementation details.
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Necessity receives unusually substantive negative controls, with a cleaner confirmatory test. The two referring/query-span sets exceed all 250 layer-matched random sets, with Holm-adjusted significance across 12 settings (Tables 3 and 10). Image-heavy heads and several generic-damage controls do not reproduce their NCS (Appendix A.4, Table 12). Importantly, the authors acknowledge that the mismatched-image arm does not itself cancel generic damage. The separate equal-sized-cell masking contrast addresses this limitation more directly: all eight query-span/output-token sets score 0.181-0.381 against approximately zero random means, while last-token effects are at most 0.007 (Table 16). Together, these checks support a real distinction between the tested discovery settings, beyond high image attention alone.
Critical weaknesses
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The steering result is convincing at the specified intervention strength but does not yet support a broader judgment about steering-based validation. The default bias is beta = 10,000 (Eq. 2), while the pilot already shows substantially different behavior at beta = 3: referring/query-span CERS reaches 0.869 and 0.789, exceeding every sampled control (Appendix A.10, Table 18). Only five random sets and four settings are tested there, so the pilot cannot establish specificity either. Section 6 appropriately qualifies the conclusion, but whether the observed random-control problem primarily reflects extreme intervention strength remains unresolved. This matters because steerability is one of the paper's central contrasts. A properly controlled strength sweep is a fixable experimental gap; the strong-steering result itself remains informative.
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The broader validation is less secure than the central experiment, and NCS exposition needs clarification. Tables 7-8 and 23-24 use one random draw per set, precisely the practice criticized for steering in Section 5.2; item-level intervals do not quantify variation across random head-sets. The out-of-domain audit identifies weak oracle performance and above-chance mismatched arms. Appendix C reports that calibration brings four of five problematic mismatched arms near chance, but evaluates head-sets with the uncalibrated pipeline (Table 22). These extensions are therefore suggestive rather than equally strong replication. Separately, Section 3.3 displays the grid estimator, while Table 3 uses matched/mismatched single-image NCS. Figure 8 supplies that definition, and Appendix A.3 analyzes its arms, but Section 3.3 does not clearly introduce both estimators; Appendix E.1 still refers to "Eq.??". These fixable limitations motivate soundness 2 and presentation 2 without outweighing the controlled discovery and clean-grid results supporting weak acceptance.
Questions for authors
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[Clarification] Can the Table 18 strength sweep be expanded to enough layer-matched random draws for corrected inference, with strength selection separated from evaluation? Would the conclusions about steering specificity hold at moderate strength (Appendix A.10)?
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[Clarification] Do the cross-model necessity separations survive repeated random controls and evaluation restricted to benchmarks passing the audit? Appendix C identifies which datasets drive the pooled separation; could quantitative per-dataset effect sizes and uncertainty establish whether the effect is broad or concentrated (Tables 22-24)?
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[Clarification] Could Section 3.3 explicitly distinguish its grid estimator from the matched/mismatched estimator defined in Figure 8 and mapped to experiments in Table 28? Please confirm that the 0.083 factor contrast uses the latter throughout, so its interpretation does not rely on within-item region masking cancellation (Section 5.2).
3 comments
part 2/2
Q2. Do the cross-model necessity separations survive repeated random controls and audit-passing benchmarks? Are the effects broad or concentrated?
They survive. 20 random sets per head-set:
| Model | Benchmarks | Calibrated | Query-span and output-token sets above all 20 | Their NCS | Random mean |
|---|---|---|---|---|---|
| Qwen3-VL-8B | all eight | no | 4 of 4 | 0.14–0.22 | 0.02 |
| Qwen3-VL-8B | audit-passing | yes | 4 of 4 | 0.23–0.36 | 0.03 |
| Qwen3-VL-4B | all eight | no | 5 of 5 | 0.14–0.21 | 0.01–0.02 |
| Qwen3-VL-4B | audit-passing | yes | 5 of 5 | 0.13–0.27 | 0.02–0.03 |
Audit-passing means CountBenchQA, MMStar and ImageNet. This rule was fixed before the run.
Broad, with one large contributor. Per benchmark, on Qwen3-VL-8B:
- The two referring + query-span sets beat all 20 random sets on 8 of 8 and 7 of 8 benchmarks.
- The two ordinal + query-span sets do so on 6 of 8.
- CountBenchQA gives the largest share of the pooled difference (39–62%), then MMStar (11–19%).
So the effect is present on most benchmarks, and the pooled number is lifted by CountBenchQA. The new per-benchmark table in Appendix C gives every value with its interval.
Last-token sets stay small out of domain: 0.007 and 0.047, against 0.14–0.22 for query-span sets. One of them (co-ref-last) is above its random sets, mostly because of CountBenchQA. The paper now says that the last-token null holds on ImageNet and is approximate out of domain.
Q3. Could Section 3.3 distinguish the two estimators? Please confirm that the 0.083 contrast uses the matched/mismatched one throughout.
Confirmed. The 0.083 contrast uses NCS-MCQ throughout. Recomputed from the saved outputs: 0.083 [0.057, 0.109], two-sided, paired over the 400 items. It uses no region masking, so it does not rely on cancellation inside items. Its controls are random sets (about 0), damage-built sets (at most 0.025) and the text-solvable arm (Table 12).
The grid test gives the same contrast on its own: 0.283 against 0.004 (Table 6). Sec. 3.3 now defines both tests, and Table 28 names the test for every result.
Both gaps you named are now closed, and the steering result has a mechanism behind it. We hope this strengthens your support for the paper.
Dear Reviewer Fu4v,
Thank you again for your constructive review. The discussion period ends tomorrow, so we wanted to check whether our response answered your questions.
Both gaps you named are addressed with data. (1) Strength sweep, with strength selection separated from evaluation: was fixed in advance, and on new items all four query-span sets beat all 250 random sets; at none does. (2) Repeated random draws: out of domain on Qwen3-VL-8B and Qwen3-VL-4B, with 20 random sets per head-set and with and without calibration, every query-span set beats all of them on necessity. We also found the mechanism: at the answer position, the default edit leaves steered heads with no attention on text, and keeping it restores the separation.
If these results strengthen your view of the paper, we would be grateful if you would consider reflecting that in your score.
part 1/2
Thank you for the detailed review. You named two gaps as fixable: the steering strength and the single-draw tables. Both are now closed with data. We follow the order of your review.
W1. Is the random-control problem a product of extreme steering strength?
It is resolved: yes, and we can show the mechanism.
Sweep. All 12 settings, 20 random sets each, N=200:
Mechanism. At β=104 the edit takes all attention away from text. A steered head puts 0.00 on text and 0.999 on the target cell, whether it was discovered or random. Every head-set becomes the same hard pointer.
Test of the mechanism. We steered at β=104 but kept each head's text attention fixed (four settings, 20 random sets, N=200). Discovered sets then beat all 20 random sets in 4 of 4 cases (original edit: 0 of 4). The spread of random sets falls from SD 0.22 to 0.08. A boost-only edit, which also removes text attention, fails again (0 of 4). A suppress-only edit, which keeps it, works (4 of 4).
The strong-steering result stays in the paper, as you suggested, because that is the strength prior work reports. The paper now adds the explanation and the fix.
W2. Broader validation and NCS exposition
(a) Single random draws in Tables 7–8 and 23–24.
Rerun with 20 random sets per head-set on Qwen3-VL-8B and Qwen3-VL-4B. The necessity result holds on both (Q2). Gemma-4, Ovis1.5 and InternVL3.5 are not rerun yet and stay labelled as single-draw. Qwen3.5-9B is removed, because no fair control exists when top-100 covers 78% of its heads.
(b) Calibration.
Done. Every new run is evaluated with and without calibration, and on the audit-passing benchmarks alone. The result is the same in all four cases (Q2).
(c) NCS exposition.
Done. Sec. 3.3 now gives NCS-MCQ and NCS-grid as two named equations, and the reference in Appendix E.1 is fixed.
Q1. Can the sweep be expanded to enough random draws for corrected inference, with strength selection separated from evaluation? Would the conclusions hold at moderate strength?
Yes. Selection and evaluation used different data.
With 100 sets, a two-sided Holm test over four settings cannot reach 0.05 even when every random set is beaten. That is why the extension to 250 was planned. On the same items and sets at β=104, 0 of 4 beat their random sets.
Moderate strength. The original conclusion holds from about β=10 upward: 2 of 12 sets beat all 20 random sets at β=10, 1 of 12 at β=100, 0 of 12 at 104. It reverses at β≤3 (9 of 12).