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Under review as a conference paper at ICLR 2027

When Does Covariance Minimize the Expected Maximum Edit Response?

Abstract

Covariance-based knowledge editors choose an update direction by minimizing its mean squared response on unrelated inputs. A small mean square can hide a large response among the probes that evaluate the edit. We ask when the same direction also minimizes the expected largest absolute response over a finite probe budget. In a fixed feasible subspace, covariance placement is optimal for every nonzero target and every number of iid probes exactly when the symmetrized whitened activation law is spherical. Centered elliptical laws with finite covariance meet this condition, including laws with polynomial tails. Bounded laws with the same covariance can need different directions at different budgets. A dimension-free converse turns measured directional anisotropy into a lower bound on the worst-target risk ratio. The remaining gain depends on the target. In 32-dimensional target-conditioned slices from five architectures, the median held-out risk ratio of covariance placement to a fitted alternative at 128 probes is 2.20 at searched worst targets and 1.048 at real edit targets. On ROME's edits in two architectures, budget-fitted placement replaces the quadratic objective. It has lower geometric-mean held-out risk than ROME and a matched quadratic refit at every evaluated budget at or above its fitting budget, with rewrite accuracy unchanged. For response magnitude, fitting an empirical Weibull shape parameter raises the held-out coverage of the fitted sub-Weibull predictor from 90.1% to 97.9% at 5,000 probes.

Primary area:
learning theory
Keywords:
knowledge editing, model editing, locality, expected maximum, covariance placement, spherical symmetry, activation geometry, sub-Weibull tails, ROME

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_CkvcOpenReview ↗
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2
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Paper summary

This paper studies covariance-based knowledge editors, which choose the update direction by minimizing the mean squared response on unrelated inputs. It asks when this direction also minimizes the expected maximum absolute response over a budget of M probes. Theoretically, it shows this holds for every target and budget exactly when the symmetrized whitened activation law is spherical (Theorem 1), and gives a dimension-free bound linking measured directional anisotropy to the worst-target risk ratio (Theorem 2). Empirically, across five architectures, activations are anisotropic: covariance placement is about 2.2x worse than a fitted alternative at searched worst-case targets, but only about 4.8% worse at real edit targets.

Critical strengths

This work provides a strong theoretical analysis of when covariance-based placement minimizes the expected maximum edit response. However, the logical flow of the paper makes it difficult to follow as a whole.

Critical weaknesses

Beyond the presentation weakness, my main concern is the practical significance of the method. The reported gains are confined to a layer-level metric and are modest. I see no clear evidence of a downstream behavioral benefit: rewrite and paraphrase accuracy are essentially unchanged, and neighborhood accuracy improves by only 7–11 prompts out of 1,500. The caption of Table 21 notes that the two ROME baseline runs themselves differ on 12 neighborhood prompts, so this change appears to be of the same order as run-to-run variation.

Questions for authors

Can the authors show that the reduced layer-level response leads to a measurable improvement in specificity?

Reviewer_q9DAOpenReview ↗
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Informativeness
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Paper summary

Covariance-based knowledge editors (ROME, MEMIT, AlphaEdit) choose the key direction of an update by minimizing its mean squared response v⊤Σψvv^\top \Sigma_\psi v on unrelated inputs, subject to a gain constraint on the target key. The paper asks when this direction also minimizes the expected maximum absolute response over MM probes, RM(z)=Emax⁡i≤M∣z⊤Xi∣R_M(z) = \mathbb{E}\max_{i\le M}|z^\top X_i|, in the whitened feasible subspace.

The theoretical results are:

  • Theorem 1. The covariance direction zΣ=a/∥a∥22z_\Sigma = a/\|a\|_2^2 is optimal for every nonzero target and every iid budget MM if and only if the symmetrized whitened law εX\varepsilon X is spherical. Centered elliptical laws, including heavy-tailed ones, qualify; bounded laws with identity covariance can require budget-dependent directions.
  • Theorem 2. A dimension-free quantitative converse, κM≤CM≤exp⁡Φ(log⁡κM)\kappa_M \le C_M \le \exp\Phi(\log\kappa_M). It turns measured directional anisotropy CMC_M into a certified lower bound on the worst-target risk ratio κM\kappa_M.
  • Theorem 3. A sub-Weibull/Orlicz union bound on the maximum response, with a matching lower bound on the Orlicz ball.

The empirical results are:

  • Real activations. In 32-dimensional whitened slices over 17 architecture–layer cells in five models, the median held-out ratio of covariance placement to a fitted alternative at M=128M = 128 is 2.20 at searched worst-case targets but only 1.048 at real CounterFact edit targets.
  • Budget-fitted placement for ROME. A placement fitted by linear programming (LP) on 150 ROME requests in GPT-J and Llama-3.1 lowers held-out expected-maximum risk by 1–6.6% at every evaluated M≥MfitM \ge M_{\text{fit}}, while rewrite accuracy is unchanged.
  • Response magnitude. A fitted sub-Weibull predictor B^M=K^w(2log⁡M)1/θ^\hat B_M = \hat K_w (2\log M)^{1/\hat\theta} raises held-out coverage from 90.1% (fixed θ=2\theta = 2) to 97.9% at M=5,000M = 5{,}000.
Critical strengths
  1. Theorem 1 is a clean, correct characterization. The proof reduces optimality across targets to radiality of RMR_M, using Euclidean orthogonality implying Birkhoff–James orthogonality. It then identifies the law of every projection from its expected maxima (Hoeffding), and passes to sphericity via a Cramér–Wold argument. The counterexamples in Appendix J.4–J.5 show that both "all budgets" and "iid probes" are needed, which is a nice touch. I checked the main steps of the proofs of Theorems 10 and 11 and found no errors.
  2. Theorem 2 adds something to the stability literature. It gives an explicit, dimension-free bound with the right λ\sqrt{\lambda} order as κ→1\kappa \to 1, where the existing constant-factor bound C≤12κ+3C \le 12\kappa + 3 is vacuous below C=15C = 15. It also covers the polyhedral norms that finite probe banks induce.
  3. The empirical methodology is unusually careful. Fit and evaluation halves are article-disjoint, LP solutions carry certified optimality gaps, and a spherical null reference keeps each slice's radii while randomizing directions. Bootstrap intervals resample at the cell, architecture, request, and article levels. The paper also runs a matched quadratic refit that isolates the objective from the fitting probes and affine family.
  4. The reporting is candid. The paper states that real-target gains are small, that LP is worse than ROME below its fitting budget, and that fitted structure fails to transfer across an article boundary on contiguous caches. It also reports that the deployed θ^\hat\theta estimator does not recover the true tail index.
Critical weaknesses
  1. The practical significance is small and not tied to editing outcomes.

    • Real-target gaps are small. At real edit targets, the median gain of the fitted alternative is about 5% at M=128M = 128 (held-out HM=1.048H_M = 1.048). The headline 2.20 is attained only at adversarially searched targets that are nearly orthogonal to real ones (median ∣cos⁡∣=0.014|\cos| = 0.014 vs. 0.127 under the spherical reference), so it says little about editing.
    • LP's gains are budget-specific. LP improves ROME by 1–6.6% at M≥MfitM \ge M_{\text{fit}}, but is worse below its fitting budget: ROME/LP is 0.859 at M=32M = 32 for Mfit=512M_{\text{fit}} = 512.
    • Behavior barely changes. Rewrite accuracy is identical. Neighborhood changes by 7–11 of 1,500 prompts and paraphrase by at most 1 of 300, with no significance test.
    • The objective is never connected to harm. The paper motivates the expected maximum by noting that a small mean square can hide a large response on some probes. It never shows that the expected maximum of a layer-level projection relates to downstream locality failures, specificity, or any model behavior. Without that link, it is unclear why an editor should optimize this quantity rather than the mean square, a quantile, or CVaR.
  2. The probe distribution and its fragility are central but under-examined.

    • All placement results use one token per Wikipedia article, drawn from the first 128 tokens. That is a particular proxy for "unrelated inputs," and the fitted direction is specific to it.
    • The contiguous-cache experiment (Table 15) shows that when fit and evaluation probes come from different articles, the held-out ratio at the worst target falls to 0.55–0.57 and C^Meval\hat C^{\text{eval}}_M falls to about 0.21. A fitted direction can therefore be much worse than covariance placement under a modest distribution shift.
    • This deserves direct study: a fitted placement that is optimal on its fitting distribution but fragile to shift is a real deployment risk. A natural test is whether LP fitted on Wikipedia still beats ROME on CounterFact neighborhood prompts, or on another corpus.
  3. The theory characterizes an idealized regime that real activations clearly violate.

    • Theorem 1's condition does not hold in practice. It requires optimality for every target and every iid budget. Real activations are known to be strongly anisotropic and heavy-tailed (massive activations, outlier dimensions), so it is unsurprising that the "iff" fails. The interesting question is how much covariance placement loses at the targets and budgets that matter, which the theory does not address.
    • Theorem 2's floor applies to the worst-case target, not real edits. By the paper's own measurements, real targets sit far from the worst case. The "certified floor of 1.404" therefore says nothing about real targets, where the ratio is 1.048.
    • The iid assumption is not met. The iid-probe assumption that Theorem 1's converse needs (Appendix J.5) does not hold for contiguous probes, and the article-boundary result suggests this matters empirically.
  4. Section 5 is weakly connected to the rest of the paper, and its contribution is limited.

    • It answers a different question. Predicting the size of the maximum along a fixed direction is a different problem from choosing the direction. The link ("Theorem 1 ties the optimal direction to directional symmetry") is loose, and the paper reads as two studies.
    • Theorem 3 is textbook. It is the standard Markov–Orlicz inequality plus a union bound. Once θ^\hat\theta and K^w\hat K_w are estimated from data, the predictor carries no guarantee; the conformal calibration in Appendix D.3 provides one, but that is also standard.
    • θ^\hat\theta does not estimate a tail index. Table 14 shows the deployed estimator compresses true θ∈[0.5,2]\theta \in [0.5, 2] into [0.91,1.19][0.91, 1.19], and returns 0.87 on a Pareto law whose Orlicz norm is infinite for every θ\theta. The paper acknowledges this and calls θ^\hat\theta an "empirical shape parameter." Calling the predictor "sub-Weibull" is then misleading.
    • The headline coverage comparison is not matched. The abstract's 90.1% → 97.9% compares predictors at different coverage. A smaller θ^\hat\theta (median about 1.09) mechanically inflates (2log⁡M)1/θ^(2\log M)^{1/\hat\theta} relative to θ=2\theta = 2. At matched coverage, Table 12 shows the fitted-θ^\hat\theta scale is looser than fixed θ=2\theta = 2 at the median (ratio 1.083 [1.049, 1.120]) and tighter only at the 90th percentile. The simple fit-half maximum is tighter than fixed θ=2\theta = 2 at the median.
    • The second-moment baseline is a strawman. It is essentially a Gaussian bound, and it is scored on the fitting probes while the fitted predictor is scored on held-out probes (Figure 4).
  5. The experimental scope is narrow relative to the framing.

    • The abstract and introduction motivate the work with ROME, MEMIT, and AlphaEdit, but budget-fitted placement is tested only on single ROME edits at layer 5 of two models, 150 requests each.
    • It is not tested on batched or sequential editing (MEMIT, AlphaEdit), where accumulated interference matters most.
    • All geometry runs in 32-dimensional slices of a much larger input space, so the restriction itself shapes the result. Tables 17–18 show that the slice choice moves the real-target ratio by more than the effect being measured.
    • The computational cost of the cutting-plane LP per edit is not reported.
  6. Presentation makes the paper hard to evaluate.

    • The main text is extremely dense and leans on a 37-page appendix, many cohorts (canonical corpus, estimator-calibration re-analysis, stored-direction frontier, headroom decomposition, ROME placement), and a large notation table.
    • Several key definitions sit only in the appendix, including the null-normalized diagnostic DMD_M, the target search, and the LP affine family.
    • The abstract is a sequence of numbers with little context.
    • Appendix D.5 notes that 51 GPT-J cells (3,373 records) "rest on their archived summaries alone" and could not be reconciled with raw responses. That is a reproducibility concern for the coverage results.
Questions for authors
  1. Is there evidence that lowering the expected maximum layer response improves any downstream property, such as neighborhood accuracy, specificity on hard neighbors, or perplexity on unrelated text, beyond the unchanged CounterFact metrics in Table 21?
  2. How does LP fitted on the Wikipedia bank perform when evaluated on a shifted probe distribution, such as CounterFact neighborhood prompts or another corpus? Given Table 15, how should a practitioner choose the fitting distribution and MfitM_{\text{fit}}?
  3. Can budget-fitted placement be applied to MEMIT or AlphaEdit in batched or sequential settings, where interference accumulates? What are the per-edit LP compute and wall-clock costs?
  4. Why the expected maximum rather than a high quantile or CVaR of ∣z⊤X∣|z^\top X|, which would be less tied to a specific MM and possibly more robust under shift?
  5. Can the theory say anything about the ratio at targets drawn from the real target distribution, rather than the worst target? Real and worst targets are nearly orthogonal in your slices.
  6. For Section 5, can you report the coverage comparison at matched threshold size, or the matched-coverage looseness of the fitted predictor against the fit maximum and the 99.9% quantile, in the main text rather than raw coverage?
  7. How do results change at slice widths much larger than 64, closer to the full key dimension in which editors actually operate?
Reviewer_px9qOpenReview ↗
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Paper summary

The paper studies how knowledge editors like ROME choose the key direction of an edit. ROME picks the direction that minimizes the average squared response on unrelated inputs, but a small average can hide a few large spikes. The authors instead minimize the expected largest response over M probes and ask when this gives the same direction. They prove that covariance placement is optimal for every target and every M exactly when the whitened activation distribution is spherical, and that measured anisotropy gives a guaranteed lower bound on how much worse it can be. On five architectures, activations are clearly anisotropic: at searched worst-case targets, covariance placement is 2.2× worse than a fitted alternative, but at real edit targets only about 5% worse. A budget-fitted version of ROME (LP) lowers held-out worst-case leakage by up to about 7% at budgets at or above its fitting budget, with rewrite accuracy unchanged.

Critical strengths
  • The question targets a real blind spot of covariance-based editors (average vs. worst-case leakage), and the theory is clean. Theorem 1 gives an exact if-and-only-if condition, Theorem 2 turns measured anisotropy into a dimension-free guarantee, and Figure 1 makes the idea intuitive.
  • The experiments are good. They use article-disjoint held-out probes, a spherical null reference, certified LP solutions, five architectures, and fifteen editor configurations on six datasets. They also report the weak points openly: the small gap at real targets, and LP losing below its fitting budget.
Critical weaknesses
  • The practical impact is limited. At real edit targets the gap is only about 5%. LP improves worst-case leakage by at most 6.6%, only when the evaluation budget is at or above the fitting budget, and it is up to 14% worse below it. Model behavior barely changes (Table 21: rewrite unchanged, neighborhood +7 to +11 of 1,500 prompts), so it is not shown that lower layer-level leakage improves downstream locality. The editing evaluation is also narrow: only ROME, single edits, two models, one layer and 150 requests, all inside 32-dimensional slices. MEMIT, AlphaEdit and sequential editing are named as motivation but not tested.
  • The paper is hard to follow and its parts are loosely connected. The placement theory and the response-size predictor are almost separate stories, and the many metrics (κ_M, C_M, Ĉ_M, H_M, D_M) rely heavily on the appendix.
Questions for authors
  • Does lower worst-case leakage at the edited layer translate into better downstream behavior, for example neighborhood accuracy, preservation of unrelated facts, or KL divergence and perplexity on unrelated text? The differences in Table 21 are very small.
  • Worst-case leakage should matter most when many edits accumulate. Can you test sequential or batch editing (MEMIT, AlphaEdit), where the paper says the question also applies?
  • From an associative-memory view, a rank-one edit stores a new key–value pair, and leakage is crosstalk with the other keys. Does the measured anisotropy reflect clustering in the stored keys, and would choosing directions by worst-case crosstalk keep interference lower as more facts are stored?
  • In MoE models, each expert sees only the tokens routed to it, so its activation distribution is likely far from spherical. Does the analysis extend to editing an expert in an MoE model, and how does routing change the probe distribution that matters for the edit?
  • Probes exclude the first two token positions and come only from Wikipedia. How sensitive are the anisotropy and LP gains to massive activations or outlier dimensions (if those positions are included), and to other probe sources such as code or chat data?
  • LP is fitted to one budget and loses below it (0.859 at M = 32 when fitted at 512). How should M_fit be chosen in practice? Would a multi-budget or worst-over-budgets objective avoid this loss?
  • LP’s mean squared response is 14–97% higher than the quadratic refit’s. Does this hurt average-case side effects? A trade-off curve between mean-square and worst-case risk would help.
  • All placement experiments use 32-dimensional slices. How do the gains, and the LP’s compute cost compared with ROME’s closed form, scale to the full input dimension?

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