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Under review as a conference paper at ICLR 2027

DIAL M FOR MONOSEMANTICITY : RECONSTRUCTION METRICS CANNOT CERTIFY SAE BASIS QUALITY

Abstract

Reconstruction metrics are the most common way to certify a sparse autoencoder (SAE), yet any functional of the reconstruction, MSE, FVU, CE-recovered and patched task accuracy among them, is provably constant under an invertible remix of the code: it cannot tell a dictionary from one strictly more mixed in the tar- geted latent basis. We use this identity constructively, mixing the basis of one pretrained SAE post hoc with the reconstruction preserved exactly, against a clone- split control arm whose residual support confound is a step rather than a ramp and so cannot manufacture a dose-response. Reading the result requires a calibrated operating point: the identical grid returns opposite signs depending only on the steering coefficient, and at the strength our pre-registration inherited the model sits 17–31 nats of KL from unsteered behaviour. At a post-hoc strength inside the regime our diagnostics certify, increased mixing lowers top-k SAE-latent steer- ing while every reconstruction metric reports the dictionary unchanged: −0.298 [−0.509, −0.089] on irony, negative but unresolved on SNLI, and negative in 21 of 23 cells outside the broken regime. Full-set steering is provably unaffected. We recommend steering results report answer-position KL, an off-target accuracy delta, and one calibrated strength as a fraction of the activation norm.

Primary area:
interpretability and explainable AI
Keywords:
sparse autoencoders, mechanistic interpretability, monosemanticity, polysemanticity, dictionary learning, activation steering, evaluation metrics, causal evaluation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_T7UBOpenReview ↗
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2
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Paper summary

The paper constructs an invertible mixing transformation that changes an SAE's feature basis while preserving its reconstruction. It compares mixing with a clone-split control and measures probing and steering outcomes. A steering-strength analysis finds that the sign of the mixing effect changes with intervention magnitude, motivating calibration diagnostics.

Critical strengths
  1. The reconstruction-preserving construction provides a concrete test of what reconstruction metrics cannot identify. The nonnegative codes and normalized decoder rows make the intervention more informative than an unrestricted change-of-basis identity alone.

  2. Figure 3 and Table 10 show that intervention strength can reverse the comparison. This supports reporting answer-position KL and intervention magnitude. The paper also reports failed checks and withdrawn analyses rather than presenting only favorable results.

Critical weaknesses
  1. The primary outcome does not establish useful steering. Section 4 measures a raw target logit rather than a margin or probability. A common offset to all output logits can change this quantity without changing predictions or KL. Appendix D.3 reports negative absolute SAE effects and compares them with a worse random-direction baseline, but that comparison does not establish improved target preference. The strongest calibrated result resolves on irony, while several replications remain uncertain. The observed sensitivity of a selected steering direction therefore supports a narrower conclusion than degradation of basis quality or steering utility.

  2. The support and calibration evidence do not fully match the main analysis. Corollary 2 gives constant support only at positive mixing doses, while the fitted slope includes zero, allowing a support step to contribute to the slope. Removing zero leaves negative point estimates in Table 6, so this does not explain away the effect, but corresponding intervals are needed. Table 8 also reports clone support increases of 12.798 and 12.495, exceeding Stage B's ten-pair maximum. Finally, Table 11 extends calibration labels beyond the single pairing measured in Table 10 and includes BoolQ despite stating that it was not separately classified.

Questions for authors
  1. Does the effect persist for target-versus-source logit margins or target probabilities at the calibrated coefficient? How does it compare with a random rotation matched for the change in steering direction?

  2. Can you report positive-dose-only intervals, identify the experiment behind Table 8, and provide Stage B's support counts? Which cells in the cross-configuration tally have directly measured calibration diagnostics?

Reviewer_h6H9OpenReview ↗
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3
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Informativeness
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Paper summary

The paper shows that standard sae reconstruction metrics like mse and fvu are perfectly invariant under any invertible reparameterization of the latent code. so these metrics cant certify whether a basis is monosemantic or polysemantic. they build a dial to inject basis mixing while preserving reconstruction exactly. they use a clone-split control arm to account for l0 inflation and show downstream steering gets worse with mixing even though reconstruction metrics are blind to it.

Critical strengths

Their observation 1 is simple but devastating to current sae evaluation norms. formally proving that reconstruction fidelity is uninformative about basis alignment forces the field to reconsider how it evaluates dictionaries. experimental design is good. using the clone-split control to isolate the effect of basis mixing from sparsity inflation is smart

Critical weaknesses

downstream steering results are somewhat noisy and highly sensitive to the operating coefficient c. the fact that the sign of the effect can flip entirely depending on whether the model is in an intact or broken regime muddles the takeaway. mixing dial is constructed post-hoc. it bounds the sensitivity of readouts to structural mixing but it doesnt quantify the cost of natural polysemanticity that arises organically during gradient descent.

Questions for authors

Since reconstruction fails to measure basis quality did you test whether activation-side metrics or local manifold geometry evaluations can catch the injected mixing before running the expensive downstream steering checks? does the performance degradation pattern hold if you do top-k selection based on output-logit effects rather than activation-side scores?

1 comment
AuthorsOpenReview ↗

Addressing the weaknesses, and answering the questions put up.

Dear Reviewer,

Thank you for your patience. We did not hear back on the question we asked, so we have done our best to address every comment, using the activation-side and decoder-geometry measures we have. The revised PDF is uploaded; all new or changed text is in blue, and page numbers below refer to it.

1. Does the pattern hold with top-kk selected by output effect? (Q b)

Addressed. We ran two output-based selection rules, all else at the headline configuration (k=10k = 10):

  • Attribution (12 draws): latents ranked by activation change ×\times (decoder row ⋅\cdot gradient of the class-logit difference). We report it with a pre-set check it did not pass (gradient vs. measured effect, r=0.78r = 0.78 irony, 0.280.28 SNLI; threshold 0.8).
  • Measured effect (4 draws): every candidate latent (158 irony, 125 SNLI) steered on 64 prompts, ranked by activation ×\times measured label-logit effect.
Selectionirony marginSNLI marginoverlap with activation top-10
activation (paper)−0.016 [−0.039, +0.009]−0.356 [−0.472, −0.247]—
attribution+0.172 [+0.099, +0.245]−0.384 [−0.511, −0.251]7.6 of 10
measured effect+0.034 [−0.037, +0.106]−0.112 [−0.202, −0.022]7.7 of 10

On SNLI the effect holds under both output-based rules; on irony it does not, which is why the claim is now stated for SNLI. Where: App. H.5, Table 16 (pp. 34–35); Table 2 rows "Attribution-selected" and "Measured-effect" (p. 7); Sec. 6 (pp. 9–10).

2. Can cheaper metrics catch the mixing before steering? (Q a)

Addressed. New App. H.8. Some cheap checks do catch the dial:

  • Activation side: the Feature Monosemanticity Score falls with λ\lambda on all three tasks, every interval excluding zero.
  • Decoder geometry: at λ=0.45\lambda = 0.45 the two decoder rows of a mixed pair have cosine −0.979-0.979 (irony) and −0.977-0.977 (SNLI), matching the closed form −0.98-0.98.
  • Co-firing: across 44 toy SAEs with L0L_0, width and architecture fixed, co-firing among the top-10 task latents tracks code alignment (partial ρ=+0.68\rho = +0.68 [+0.36+0.36, +0.84+0.84]).

The appendix also states their limit: in the toy model, decoder coherence and co-firing flag the harmless clone control as strongly as real mixing. On manifold measures: any measure computed on the reconstruction is blind to the dial by Corollary 1, since the reconstruction does not change; only measures on the codes or the decoder can detect it. Where: App. H.8 "Cheaper detectors of mixing" (p. 36); Finding 1 (p. 5); Table 2 FMS row (p. 7).

3. Results are noisy and sensitive to the strength cc; the sign flip muddles the takeaway

Addressed. Two fixes.

  • Part of the noise was a bootstrap that did not match the paper's description. The corrected bootstrap gives intervals up to 2.6$\times$ narrower (e.g. SNLI raw logit −0.232-0.232 [−0.411-0.411, −0.073-0.073], was [−0.773-0.773, 0.1350.135]).
  • The margin makes the takeaway clean on SNLI: it falls at every strength in the headline run, and in all six configurations at strength 0.02.

Section 5 now states the rule: a steering comparison needs its strength, a validity diagnostic and a target-preference outcome; Finding 3 adds recommendation (v), report a margin. The strength-1.0 sign flip (KL 17–31 nats) is kept as the warning it was meant to be. Where: Sec. 4 bootstrap note (p. 7); App. F (p. 31); Sec. 5 and Finding 3 (p. 8); Table 14 (p. 34).

4. The dial is post hoc and does not measure natural polysemanticity from training

Addressed. Agreed for the real model, and the paper says so (Finding 2, Limitations). The new toy model covers training directly, because the true features are known for SAEs trained from scratch. There, training itself produces dictionaries that reconstruct better and are worse:

  • TopK, L0L_0 6 → 24: FVU −0.090-0.090, decoder alignment on structured features −0.101-0.101 (replicated on a second world).
  • ReLU+L1, penalty 0.6 → 0.02: L0L_0 12.6 → 107, FVU 0.222 → 0.002, code alignment −0.395-0.395; repeated in three further worlds (decoder alignment −0.345-0.345 to −0.358-0.358).
  • JumpReLU: higher L0L_0 gives FVU −0.120-0.120 with decoder alignment −0.339-0.339.
  • A trained dictionary at L0=12L_0 = 12 reconstructs better than the true one (FVU −0.0055-0.0055) while being further from it (decoder alignment 0.946 vs. 1.000).

Where: App. H.7, Table 18 tests 3, 6, 7, 8, 12, 13 (pp. 35–36); Sec. 6 (p. 10); Finding 2 and Limitations (pp. 6, 10).

We would be grateful if you could let us know whether this addresses your questions, and we are happy to clarify anything further.

Reviewer_rNEXOpenReview ↗
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Paper summary

The paper presents a study of sparse autoencoders (SAEs) reconstruction quality measures from the following point of view: could a reconstruction information distinguish between bases SAE have chosen? Authors distinguish measures that could have this power and provably have not, then proceed with analyzing steering behavior under it, conducting a controllable latent remixing intervention into atoms learned by SAEs without changing the reconstruction, and analyzing when steering breaks the model.

Critical strengths

S1. The distinction between benchmark measures presented in the paper is nice and I think important to have. However, by itself it is a minor contribution.

S2. A remixing intervention is interesting way to controllably test interpretability-related SAE behavior.

Critical weaknesses

W1. Writing is heavily convoluted and unclear to extent I could not understand majority of the paper, especially the purpose of things introduced and developed. There is a lot of terms used but underfined, for example cornerstone notion of basis quality the paper builds around is never defined anywhere. The mathematics in paper seem unnecessary, many paragraphs are number and term dumps, have a lot of underfined and unfamiliar wording. All these problems likely follow the uncontrollable AI assistance in writing.

W2. On results and things I understood, my concern is that their substance is thin. First section on identifiability is, as I read it, a restatement of known identifiability problem (if you have a distribution that could be generated by different latent configurations, you cannot distinguish which one has generated it). The damage of high steering coefficients is a known phenomenon and it is unclear to me what exactly authors contribute here.

W3. Authors use real-world SAEs to conduct their experiments, but basis quality is something that could or should be evaluated with known ground truth of some form; their mixing procedure operates on top of already trained SAE and is not something that could help distinguish basis quality. Maybe the basis quality is understood differently, but there is no definition in the paper. Since SAEs are trained beforehand, no controllable variation of their properties is present beyond mixing.

Questions for authors

Q1. Can you state plainly what exactly novel and different from the prior literature? What you contribute, why it has not been shown in previous literature?

Q2. Could you test the same on toy models with use of ground truth and define the basis quality?

2 comments
AuthorsOpenReview ↗

Addressing the weaknesses, and answering the questions put up.

Dear Reviewer,

Thank you for your patience. We did not hear back on the questions we asked, so we have done our best to address every comment. The revised PDF is uploaded; all new or changed text is in blue, and page numbers below refer to it.

1. Basis quality is never defined (W1, Q2)

Addressed. Section 1 now defines it. Given ground-truth features g1,…,gmg_1,\dots,g_m, a dictionary's basis quality is how well single latents match single features, measured two ways:

  • Decoder alignment: mean over features of the best ∣cos⁡(wi,gf)∣|\cos(w_i, g_f)| over latents (MMCS, Sharkey et al. 2022).
  • Code alignment: mean over features of the best correlation between a latent's activation and that feature's coefficient.

Gemma has no ground truth, so there the paper uses an ordering that holds by construction. Example: at λ=0.3\lambda = 0.3, a latent that fired on irony cues fires as 0.7×0.7\times(itself) + 0.3×+\ 0.3\times(a negation latent). The decoder changes by the exact inverse, so every input is reconstructed bit-identically, but the blend matches neither feature as well. Larger λ\lambda means lower basis quality. The toy model (point 4) measures both alignments directly. Where: Sec. 1, "What we mean by basis quality" (p. 2); Glossary, App. I (p. 36).

2. The writing is hard to follow; terms are undefined (W1)

Addressed. We rewrote in four ways:

  • A one-sentence Purpose at the start of Sections 3–6 saying what each section establishes.
  • A glossary (new App. I) defining every term the paper coins: basis mixing, the dial, admissible, mix arm, clone-split control, τ\tau, pairing draw, sampling seed, steering strength, damage meter, regimes, margin, common offset, split pair.
  • New results are in tables (Table 2 rows; Tables 13–18), not inline number lists.
  • The definition of basis quality (point 1).

Where: Purpose lines pp. 4, 5, 7, 9; App. I (p. 36); Table 2 (p. 7); Tables 13–18 (pp. 33–36).

3. What exactly is new? (W2, Q1)

Addressed. We agree both background facts are known, and the paper now says so (Sec. 2: "that large strengths damage the model is thus known, and we do not claim it"). The contributions are three things built on them:

  1. A consequence for evaluation, not identifiability itself. Identifiability up to reparameterisation is classical (Locatello et al. 2019), and recent SAE work uses it for training (Cain et al. 2026). We apply it to evaluation: MSE, FVU, CE-loss recovered, patch-KL, accuracy after patching and an unregularised dense probe are provably constant over the orbit, so none of them can rank dictionaries by basis quality. Table 1 sorts common metrics by this.
  2. An intervention on the basis alone. Prior evidence compares SAEs that differ in width, sparsity and training run at once (Wang et al. 2025). The dial changes only the basis, keeps codes nonnegative and decoder rows unit-norm, and has a control arm matched for the sparsity side effect.
  3. A comparison between two dictionaries flips sign with steering strength. Known work shows one model degrading as strength grows; we show the comparison inverts: −0.298-0.298 at strength 0.02 (KL 0.0009–0.0066 nats) versus +12.479+12.479 at 1.0 (KL 17–31 nats). This yields four diagnostics we recommend every steering paper report, plus a fifth added in revision (report a margin).

Where: Sec. 1 "What is new here" (p. 2); Sec. 2 (p. 3); Table 1 (p. 3); Finding 3 (p. 8).

4. Test with ground truth in a toy model (W3, Q2)

Addressed. New toy model: 256 ground-truth features in 64 dimensions, sparse nonnegative coefficients, a binary task carried by 10 features. We ran 13 pre-registered tests and report all of them (Table 18).

  • Dial on a trained toy SAE: reconstruction stays constant (FVU range 2×10−82\times10^{-8}) while decoder alignment of the touched task features falls from 0.962 to 0.837 at λ=0.45\lambda = 0.45; the clone-split control stays flat.
  • SAEs trained from scratch, no dial: raising a TopK SAE's L0L_0 from 6 to 24 improves reconstruction (FVU −0.090-0.090) while decoder alignment on structured features falls by 0.101; replicated on a second toy world and with ReLU+L1 and JumpReLU SAEs.
  • Which readout tracks quality: across 44 toy SAEs with L0L_0, width and architecture fixed, reconstruction does not track decoder alignment (partial ρ=+0.19\rho = +0.19 [−0.38-0.38, +0.57+0.57]); the steering margin does (+0.61+0.61 [+0.15+0.15, +0.77+0.77]).

10 of 13 tests support the claim; Table 18 also reports the 3 that do not. For example, across 27 normally trained ReLU SAEs, reconstruction and quality correlate (ρ=+0.82\rho = +0.82) because training improves both together. The dial shows why that correlation is not a certificate: it moves quality at fixed reconstruction. Where: App. H.7, Table 18 (pp. 35–36); Sec. 6 "Ground truth in a toy model" (p. 10); Contribution 5 (p. 2); Conclusion (p. 10).

Please let us know whether this addresses your concerns; we are happy to clarify anything further.

Thank you for your thorough revision.

Historically, papers were written for a human reader, and authors of good papers usually had a model of how reader will perceive the text and what their attention span would be, and how to manage it well across the paper. With modern state of AI, this might be no longer the case. Adding a definition requires placing it appropriately, at the time it does work, and with intention that the reader will carry that definition throughout the paper, and those placements follow the mental model of how potential reader will go through the text, so writing was focused. The same goes for results, tables, exposition, scene-setting and so on.

My commentaries concerned writing as a whole, while the revised version, as it seems, aimed to resolve my concerns mechanically: by adding a glossary, by writing a separate out-of-place paragraph for basis quality definition, by extending the already dense Table 2, by adding a formal "Purpose: ..." sentence, by adding some toy model runs with unclear design choices (H.7) and putting a dense table that needs effort to understand what is happening, and so on, while the problem underlying that remains untouched - paper needs proper contextualization of every unfamiliar word instead of just adding more information, maintaining the lowest possible amount of effort for the reader to be able to comprehend the material of the paper and building it gradually, avoiding unnecessary jargon and relying on well-known plain English words and scientific terms that need no specific effort from a reader to parse it, and presenting the results in a form that makes reasons and hidden meaning accessible. Of course, the paper does not need to be accessible for everyone, but in its current version, everything is simply scattered and improperly placed to extent that it appears being written for AI reading.

On the results themselves, "none of them can rank dictionaries by basis quality" - I think that they need not since they do not consider underlying basis as observable, and this creates issue whether we can identify "good" and "bad" SAE basis at all. Thus I see toy model study as a preliminary for studying the basis quality in real-world LLMs. Considering toy models, H.7 presents very unclear toy model that combines hierarchy, some "binary task", correlation and so on; since it is a model of what generates the hidden states, I think single toy model is not enough and some controls are needed; each control should aim at ruling out alternative explanations, and I cannot provide any of them right now. What toy model actually added was not quite clear to me. Increase of reconstruction quality with increasing sparsity is well-known effect, and it drifts away from faithfulness.

I maintain my view on the paper and I think a major rewrite is required here, with focused exposition. I suggest to focus on what was actually unknown in prior literature and putting effort to deepen results in it, not restate consequences of identifiability issues. Steering seems as a good candidate - the finding that it can decide whether SAE learned faithful representations is perhaps nice and I think it could be foregrounded and deepened.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Grateful to all the reviewers. General response to each reply.

We thank the three reviewers. The revised PDF is uploaded; all new or changed text is in blue. The reviews converge on three requests, and the revision meets each one:

  1. A steering outcome that measures which answer the model prefers, with a control separating basis mixing from any change of steering direction (T7UB, h6H9). The target-minus-competitor margin is now the primary outcome, and a new equal-angle random-rotation control is added.
  2. A definition of basis quality, and ground truth (rNEX, h6H9). A definition in Section 1, and a toy model with known features in App. H.7.
  3. Clearer writing (all three). A one-sentence purpose at the start of Sections 3–6, a glossary (App. I), and new results in tables rather than inline lists.

Reproduction first. Every new run first recomputed the stored results it shares with the submission: all 832 stored cells reproduced exactly (maximum deviation 0; App. H.1, p. 33).

Errors we found ourselves (all listed in App. F, Table 12, p. 31):

  • seeds 123/999 are sampling seeds, not training seeds (same SAE);
  • the bootstrap now matches the one the text describes, giving narrower intervals (irony −0.298 [−0.389, −0.205], was [−0.509, −0.089]);
  • the Braun et al. citation is corrected;
  • the App. D.3 random-baseline sentence is withdrawn;
  • the D.2 rescaling statement is corrected for split pairs.

Decided before any new result was seen: the margin is the primary steering outcome (the raw target logit is kept, labelled pre-registered), and the claim is the one T7UB proposed: top-kk SAE steering is sensitive to basis mixing.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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