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Under review as a conference paper at ICLR 2027

Perfect Reconstruction Cannot Show Whether Two Codebooks on a VAE's Latent Space Agree

Abstract

Many systems read the latent space of a variational autoencoder (VAE) as discrete codes, and rely on each latent being read back as the code it was written as. Shannon (1948) took such a shared codebook as given; inside a VAE nothing enforces it. We prove that no item of a standard training report can reveal whether the written and read codes agree on encoded data. We construct two VAEs that reconstruct every input perfectly, infer exactly, and match on every per-example ELBO and every code histogram, yet agreement is one in the first and zero in the second. We then show that the ELBO's own terms bound how far a measured agreement can move: the variational gap bounds the shift to exact inference, and the rate bounds the shift to generation from the prior. For Gaussian posteriors, a mean-field encoder pays an exact price in the gap that depends on its choice of axes. On probabilistic PCA the gap certifies a trained encoder in all 75 settings we test, at agreement between 0.76 and 0.97. On 240 trained VAEs, a floor set by the rate and the dataset size rules out rate-side certification in advance for 66 models, and none of them certifies. The results yield a simple protocol, Certify-or-Measure, for any pipeline that reads a VAE as codes.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Variational Autoencoders, ELBO, Discrete Latent Codes, Codebook Agreement, Non-Identifiability, Certified Bounds, Information Theory, Evaluation of Generative Models

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_DtHPOpenReview ↗
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Paper summary

The submission examines the connection between discrete codebooks that partition the latent space of a VAE. Under what conditions can we know if two codebooks agree? A worked counterexample demonstrates that standard metrics reported during training (such as per example KL or ELBO) can match while codebooks differ. The paper then establishes bounds on agreements of codebooks under different sampling measures (eg agg posterior and prior) to these standard metrics -- the KL and ELBO gap. Experiments on MNIST and SVHN lend support to the bounds.

Critical strengths

None

Critical weaknesses

The submission is poorly motivated and poorly written.

It comes as no surprise that codebooks on top of a VAE's latent space -- codebooks with no relation to training, nor specifics about their definition that might serve to link them in any way -- can disagree while the VAE functions perfectly. With a careful construction and a more subtle argument, there could be a successful hook for this work, but instead it's delivered in dramatic flair characteristic of AI-packaging. In the abstract: "Shannon (1948) took such a shared codebook as given; inside a VAE nothing enforces it." Well, yes, the codebook has only as much of a connection to the VAE as is integrated into its construction, and the only details about codebook creation before the empirics is "In applications, cencc_{enc} is fit on encoder statistics and cdecc_{dec} is a nearest-prototype rule in the decoder's Bregman output geometry." (L167). Loosely, I cluster z and I cluster x, and then compare both in z by the preimage of the latter. Without some sort of conditioning on the clustering schema, I would never expect guarantees on the agreement of the clustering assignments besides what might arise downstream of (dis)agreements of the sampling distributions, which are connected to the VAE optimization.

The prose and figures are typical of AI outputs -- a sales pitch that impedes a close reading.

Questions for authors

Can the authors propose specific scenarios where the codebooks are constructed jointly with the express purpose of agreement, and demonstrate limits exist?

1 comment
AuthorsOpenReview ↗

Reply to Reviewer DtHP, updated for the revised PDF

The construction, which the submitted main text did not state. You asked for scenarios in which the codebooks are constructed jointly, and for limits. In our VAE experiments the two maps are linked, and Section 2 of the revision now says how: centers μ_k are fitted to encoder means; the encoder-side code of a latent is its nearest center (or most probable mixture component); the output prototypes are the decoded centers g(μ_k); the decoder-side code is the nearest prototype of the decoded latent. Both codes carry the index of the center. Before the experiments, the submitted main text said only that the maps are taken as given, that c_enc is fit on encoder statistics and that c_dec is a nearest-prototype rule (the sentence you quote); neither it nor Section 6 said that the prototypes are the decoded centers or that both codes carry the center's index. That omission was ours.

Jointly constructed codebooks (new Theorem 1(III)). Shared prototypes are a joint construction, though not one built for agreement. A construction built for agreement, c_enc := c_dec, has agreement one for every decoder; its limit is a cost (one decoder pass per written latent), not a failure of agreement. For the shared-prototype construction of our experiments there is a limit. Let both maps be rebuilt from each model by this rule in its k-means form (globally optimal centers; the output side read in squared distance or in Bernoulli KL, the two divergences of our experiments). Then there are two models with the same data law and prior, perfect reconstruction, exact inference and a generative law equal to the data law, with the same centers and the same encoder-side map, that match on items (m1)–(m6) of Definition 1 and have agreement 1−1/n and 1/n, for any odd n ≥ 3 (Appendix A.7, with an exact verification script). The second model exchanges, in each block of the latent space, the datum at the center with a datum of another class, so the decoded center, and with it the code read for the rest of the block, changes class. Sharing indexed prototypes therefore does not make agreement visible in the training report. Agreement does hold for every decoder if the written code is itself read through the decoder, as above, or if only the centers themselves are decoded, as in a VQ-VAE (Appendix A.7, remarks (a) and (b)). The decoders of the pair are piecewise constant, the statement is for the k-means rule, and we do not claim that training produces such pairs.

On "no surprise". For Theorem 1(I) your reading is right, and the revision says so. Its two maps are fixed and do not depend on the model, and one of them is not a readout of the decoder's output (Appendix A.1 and A.3, Table 2). We also state that its pair is not well specified (the generative law puts mass 1/K on the data) and that some misfit is necessary: by the new Corollary 1, a well-specified model with exact inference has the same agreement on encoded data and under the prior, so two such models with a common prior and common fixed maps cannot differ in agreement. Part (III) is the statement for maps that are linked to each other and to the model, and its pair is well specified.

On guarantees. We agree that the guarantees are of the kind you describe. Theorem 2 bounds how far agreement can move between sampling laws by KL budgets, and the budget alone does not establish high agreement: a certificate also needs the measured agreement. The revision adds that, given only the measured agreement and the budget, the band cannot be narrowed (Section 4).

Presentation. We removed the Shannon sentence and the historical framing, rewrote the abstract, introduction and conclusion as plain statements, and removed claims that went beyond what is proved or measured ("no item … can reveal", "trained models behave as the theory predicts", "best previously available"). The prose was drafted and revised with LLM assistance and the figures are drawn by scripts written with it; the AI-use statement, which we have made more specific, discloses both.

We would welcome your view on whether Part (III) answers your question, and on what else you would need to see.

Reviewer_2Ds6OpenReview ↗
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Paper summary

The paper investigates a disagreement between the latent codes of a single data instance seen from the perspective of code mappings underlying the encoder and decoder distributions in VQ-VAE models. The authors' position is that the codes can disagree when read by these two mapping mechanisms and propose theoretical results to support this observation, trying to construct a theoretical framework that considers all elements necessary to isolate the behavior behind this phenomenon, such as per-example reconstruction and rate terms of the ELBO objective, among many (perhaps redundant) others. They partially demonstrate their theoretical findings on small image datasets, repetitively training a few hundreds of VQ-VAEs whose encoder and decoder architectures are based on convolutional neural networks.

Critical strengths

The idea is interesting, yet hard to accept (see below).

Critical weaknesses

The rejection is based on the following two major issues that can hardly be corrected without a major revision.

  1. This disagreement should not appear in the original VQ-VAE formulation (van den Oord et al., 2017), where the code mappings underlying the encoder and decoder distributions are the same, and hence should always read the same code index for a given image. This can happen for certain constructions, such as those used by the authors, where the mappings are designed with different mechanisms, but there is no need to see these disagreements as a problem. The authors should first demonstrate the impact of this disagreement in practical applications so that investigating this phenomenon becomes important. The importance of this investigation and the impact of neglecting it is currently not covered in the paper.

  2. The whole paper is very difficult to follow. It overflows with mathematical symbols (unnecessary in many cases) even from a perspective of pure mathematical papers. Many symbols that are essential for understanding the key theoretical results are undefined, most notably qˉC\bar{q}_C that is crucial for understanding Theorem 1. A\mathcal{A} is overloaded so many times that the reader gets lost in the first reading (probably even after a few more readings). There are many poorly written sentences (e.g., "The maps are taken as given."). The form of the experimental section is also very hard to follow. The text overflows with numbers that are not connected to any experimental figure or table. The paper is repetitive in a rather inappropriate choice of words, including "certifies" and "licenses". Various references, such as Banerjee et al., 2025, are very vaguely used, suggesting that the claim tight to these references is rather unrelated. The paper uses many concepts and terms in the abstract and introduction that were never defined and read rather difficult, such as "standard training report" (what does it mean?). Many of these terms are defined only vert late in the following sections.

Questions for authors

See above.

1 comment
AuthorsOpenReview ↗

Clarification and reply: continuous-latent VAEs, not VQ-VAEs

Scope. We agree that a standard VQ-VAE passes the embedding selected by the encoder to the decoder, so the code passed across that interface is unchanged. All our models have continuous latents: convolutional VAEs and probabilistic PCA. Two code readouts are applied after training, and neither quantizes the latent that the decoder receives. The submitted introduction listed VQ-VAE tokenization among the motivating pipelines and drew this distinction only in passing, which invited the reading in the review. The revised abstract and introduction state the model class and both readouts, and Section 2 gives the two rules as formulas: the encoder-side code is the nearest fitted center (or most probable mixture component) of the latent, and the decoder-side code is the nearest decoded center of the decoded latent.

Practical relevance. We agree that the impact should be shown. The revision reports three things. (1) Our registered analysis of one interface, code-addressed generation, was negative: across models, agreement under the aggregate posterior or the prior did not predict the interface's accuracy better than standard diagnostics. (2) A further analysis of the same checkpoints, with its reading fixed before the full run (Section 6.4, Appendix D.9): within a model, generated samples whose code the decoder-side map reads back are classified as the requested class with median accuracy 0.68 against 0.25 for the rest on FashionMNIST and 0.71 against 0.31 on MNIST, in 72/72 and 24/24 configurations. On SVHN and CIFAR-10 the registered reading is negative. (3) Proposition 3 states what agreement can and cannot decide about such a task. This is one interface on small image datasets; a benefit of auditing agreement in other applications remains undemonstrated.

Presentation. In the revised PDF:

  • the abstract lists the diagnostics meant by "standard training report", and Definition 1 enumerates them;
  • q̄_C is defined at first use (Section 2);
  • "The maps are taken as given." is replaced by the definition of the two readouts and a statement of which results hold for fixed maps and which for maps rebuilt from each model (Section 2, Table 2 in Appendix A.3);
  • Table 1 ties each experiment to its population, sampling laws, criterion and result, including the negative ones;
  • "certify" now means the protocol's band with its confidence statement; a width test at a point estimate, and a band from an unlicensed budget, are called admissions;
  • Banerjee et al. (2005) is cited only for the Bregman nearest-prototype rule;
  • agreement is defined once, as 𝒜[μ] for a sampling law μ; A_q and A_prior are its two cases in the main text, and 𝒜(C), 𝒜(T) are shorthands for 𝒜[q̄_C] and the diagonal mass of a table (Section 2); the configuration C_τ of Theorem 1(II) is now described where it is used;
  • one part of Theorem 1 is now stated in the appendix, and each construction is described in words after the theorem;
  • Figure 1 is redrawn: it shows the latent space with its indexed centers, the decoder, and the output space with the decoded prototypes, so that both readouts and their shared indices are visible; the labels of Figure 2 are corrected.
Reviewer_2EguOpenReview ↗
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Paper summary

This paper investigates whether standard VAE evaluation metrics, such as reconstruction performance and the evidence lower bound (ELBO), can determine agreement between two discrete code maps defined on the same latent space. The authors consider encoder-side and decoder-side code maps and present an impossibility result showing that two VAE configurations can achieve identical evaluation statistics, including perfect reconstruction, while having completely different codebook agreement.

The paper further derives information-theoretic bounds based on the variational gap and KL rate to constrain changes in agreement under exact inference and prior sampling. Based on these theoretical results, the authors propose a Certify-or-Measure framework and evaluate it using probabilistic PCA and VAEs trained on several image datasets.

Critical strengths
  • The paper addresses an interesting question about the limitations of standard VAE evaluation metrics in assessing properties of latent representations.
  • The theoretical analysis provides a specific impossibility result and information-theoretic bounds for codebook agreement. The proposed certification framework offers an interesting perspective on evaluating latent representations.
  • The paper includes extensive experiments across different models and datasets, including analyses of the conditions under which certification is possible.
  • I appreciate the transparent reporting of negative experimental results, including unsuccessful replication experiments and the sensitivity of agreement to codebook construction.
Critical weaknesses
  1. Novelty of the central impossibility result My main concern is the novelty of Theorem 1 relative to existing work on latent representation non-identifiability. It is already well established that different latent representations can achieve identical reconstruction performance and ELBO. For example, Mathieu et al. (2019) demonstrated the rotational invariance of the β-VAE objective under an isotropic Gaussian prior, showing that different latent representations can yield the same objective value, while Locatello et al. (2019) and Khemakhem et al. (2020) studied broader identifiability limitations. I understand that Theorem 1 provides a more specific result by considering agreement between two code maps while preserving a broader set of evaluation statistics. However, I find it difficult to identify what fundamentally new theoretical insight this provides beyond established non-identifiability results.

  2. Motivation and interpretation of codebook agreement I am not fully convinced by the motivation for expecting agreement between the encoder-side and decoder-side code maps. In the experiments, the encoder-side map is constructed using a Gaussian mixture model fitted to latent representations, whereas the decoder-side map uses nearest-prototype assignment in the decoded output space. Although these constructions are related through the learned model and prototypes, they use different criteria for assigning codes. Therefore, it is not immediately clear why agreement between these two mappings should necessarily be expected. I understand that the theoretical framework allows arbitrary fixed code maps, but the practical significance of agreement between these particular constructions remains unclear to me.

  3. Sensitivity to codebook construction The experimental results suggest that codebook agreement is sensitive to how the code maps are constructed. In particular, the authors report that fitting the encoder-side GMM to posterior means while evaluating agreement on posterior samples can produce substantial discrepancies. Refitting the GMM using posterior samples reduces these discrepancies. I appreciate that the authors identify and investigate this issue. However, it raises questions about how much of the observed disagreement reflects properties of the learned VAE and how much is introduced by the codebook construction and fitting procedure.

  4. Experimental evidence and practical significance Although the paper provides extensive experimental analysis, I find the evidence for the practical usefulness of the proposed framework less convincing. The initial MNIST experiment demonstrates a substantial decrease in agreement under prior sampling, but none of the four preregistered replication conditions reproduces the finding. Furthermore, although the certification procedure succeeds on 131 of the 240 evaluated VAE configurations, most successful certificates correspond to low agreement, and the certified codes provide little improvement in label prediction over the majority-class baseline. These findings do not invalidate the theoretical results, and certification of disagreement can itself be useful. However, they leave open the question of whether the framework can provide useful certification for informative codebooks in practical applications.

Questions for authors
  1. Novelty of Theorem 1: Could the authors clarify how Theorem 1 differs from existing rotational invariance and latent non-identifiability results, particularly Mathieu et al. (2019) and Locatello et al. (2019)? What additional theoretical conclusion does the codebook-agreement formulation provide?

  2. Motivation for codebook agreement: Why should the encoder-side and decoder-side code maps be expected to agree when they use different assignment criteria? Could the authors provide a concrete application where disagreement between these maps causes a meaningful problem?

  3. Codebook construction and fitting: How should we distinguish disagreement arising from the learned VAE from disagreement introduced by codebook construction? Given the reported differences between posterior-mean and posterior-sample fitting, would fitting the encoder-side map on posterior samples be a more appropriate default?

  4. Experimental generalisation: Given that none of the four preregistered replication conditions reproduced the initial MNIST finding, how broadly should we expect the observed generative agreement drift to occur?

  5. Practical usefulness of certification: Can the proposed framework provide useful certificates for codebooks that retain meaningful information and achieve reasonably high agreement? What advantage would certification provide over directly measuring agreement when both code maps can be evaluated?

References

  • Mathieu, E., Rainforth, T., Siddharth, N., & Teh, Y. W. (2019). Disentangling Disentanglement in Variational Autoencoders. ICML.
  • Locatello, F., et al. (2019). Challenging Common Assumptions in the Unsupervised Learning of Disentangled Representations. ICML.
  • Khemakhem, I., Kingma, D. P., Monti, R. P., & Hyvärinen, A. (2020). Variational Autoencoders and Nonlinear ICA: A Unifying Framework. AISTATS.
2 comments
AuthorsOpenReview ↗

Reply to Reviewer 2Egu, updated for the revised PDF (1/2)

Thank you for the questions. The revised PDF changes the paper in response to each of them. We answer in your order and say what remains open.

Q1. What Theorem 1 adds to latent non-identifiability. Mathieu et al. (2019) show that the β-VAE objective is invariant to rotations of the latent representation under an isotropic Gaussian prior; Locatello et al. (2019) that disentangled representations cannot be learned without supervision unless inductive biases are placed on models and data; Khemakhem et al. (2020) that the joint law becomes identifiable up to simple transformations when a factorized prior is conditioned on an additionally observed variable. Theorem 1 rests on the same kind of symmetry, a bijection of the latent space that preserves the prior, and we do not claim that mechanism as new (Section 7). What it adds concerns two labeled readouts: one pair of configurations matches on every item of Definition 1 at once, so any estimate of agreement computed from that report is off by at least 1/2 on one of the two.

The revision adds Part (III). It still uses a prior-preserving bijection, but one that is not an isometry: for shared-prototype readouts fitted by k-means (centers fitted to encoder means, nearest center on the latent side, nearest decoded center on the output side), a rotation or any other isometry moves both maps together and leaves agreement unchanged, so the rotational invariance you cite cannot produce the pair. Part (III) gives two models with perfect reconstruction, exact inference and a generative law equal to the data law, with the same k-means centers and the same encoder-side map, that match on items (m1)–(m6) of Definition 1 and have agreement 1−1/n and 1/n, on encoded data and under the prior alike, for any odd n ≥ 3 (Appendix A.7; a script in exact arithmetic checks K ≤ 5 and n ∈ {3, 5, 7}). The only item of Definition 1 on which they differ is agreement under the prior, which is itself a measurement of agreement. The pair is idealized: its decoders are deterministic and piecewise constant and its centers are the global k-means optimum; the decoder-side code may be read in squared distance or in Bernoulli KL, the two divergences of our experiments. We do not claim that training produces such pairs.

Q2. Why the two maps should agree, and where disagreement costs something. They need not agree: the criteria differ. Section 2 now gives both rules as formulas, with a two-line example in which shared prototypes still give one latent two codes. Agreement matters for an interface that writes a code and expects that code back. Proposition 3 (Appendix D.8) states the relation: the task error of a code-addressed interface is within the labeling errors of the two sides of the rate at which the written and the read code carry different labels, and that rate is at most the rate at which the read code differs from the written one, which is the disagreement under the task's own sampling law when the written code is c_enc(z). Agreement alone therefore decides neither success nor failure.

We correct our submission on one point. The comparison reported as "72/72" in Appendix D.3 (D.4 in the revision) used two different judges on the same generated samples: an external classifier, and the majority label of the code that the decoder-side map reads. It does not compare two routings, and we withdraw the reading that it shows a cost of disagreement.

To test the question directly we ran one more analysis on the saved checkpoints, with no training and with the question and the reading fixed before the full run; Appendix D.9 lists what we had seen by then, which includes the two scores of the withdrawn comparison. Within each model, are generated samples classified as the requested class more often when the decoder-side map reads back the code they were drawn from? On FashionMNIST and MNIST, yes: in 72/72 and 24/24 configurations, with median accuracy 0.68 against 0.25 and 0.71 against 0.31. On SVHN, no: both sets are at chance. On CIFAR-10 the registered reading is negative: the median difference is 0.20, above the registered 0.10, but the difference is positive in 50 of 58 eligible configurations, below the registered 90%. The quantity is read-back under the interface's own request law, not A_q: across models 1 − A_q does not track the task error (Appendix D.9). This is one interface, and it concerns selecting among generated samples; it does not show that training for agreement improves a task. The earlier registered analysis is unchanged and negative: across models, agreement under the aggregate posterior or the prior did not predict this interface's accuracy better than standard diagnostics.

AuthorsOpenReview ↗

Reply to Reviewer 2Egu, updated for the revised PDF (2/2)

Q3. The VAE versus the codebook construction. On the same checkpoint, changing the declared map moves agreement by a median of 0.565 across four maps, while the rate-side budget does not depend on the map (Section 6.3). An audit of the 240 saved checkpoints under all four maps, run after submission (Appendix D.7; its label criterion was fixed after the band widths were known and before the label accuracies under the other three maps were computed), gives a median agreement on encoded data of 0.08, 0.32, 0.17 and 0.67 under our declared mixture (fitted on encoder means), the mixture refit on posterior draws, the mixture refit on prior draws, and k-means. Much of the low agreement under our declared map therefore belongs to that map, a diagonal mixture fitted on encoder means and read on posterior draws: k-means, fitted on the same means, has median 0.67 (Table 7). On your question whether fitting on posterior samples is the better default: it raises agreement (0.32 against 0.08) but less than k-means does, and the grid registered no claim that one map is correct, so we keep the preregistered declared map as the primary reading and report all four beside it. Agreement is a property of the (model, map) pair, and the paper asks that it be reported with its map and its sampling law (Theorem 3(c), Sections 6.3 and 8).

Q4. How broadly drift occurs. The preregistered replication stands at 0/4, and Section 6.1 is now limited to the MNIST case study. Three additions bound the answer. First, Corollary 1: d_bin(A_q ‖ A_prior) ≤ KL(q̄ ‖ p) ≤ KL(D ‖ p(x)) + gap, so drift needs model misfit or inference error, and a well-specified model with exact inference has none. Second, on the scaled grid the answer depends on the map: A_q − A_prior exceeds 0.05 in 7 of the 240 configurations under our declared map, in 95 under the mixture refit on posterior draws, and in 3 under the refit on prior draws (Section 6.1, Appendix D.4). Third, probabilistic PCA fitted to MNIST shows the drift under exact inference, so by Corollary 1 it comes from misfit there. We cannot say that the MNIST drift is common under the declared map.

Q5. Informative, high-agreement certificates, and certification versus direct measurement. Under the declared map no configuration meets both the width criterion and the label-information criterion of the post-submission audit (label accuracy at least 0.05 above the majority-class rate, agreement above chance). Under k-means, 41 configurations from 24 distinct VAEs meet both, at measured agreement between 0.365 and 0.814; under the stricter bar of the grid's original precommit (label accuracy at least 2/L), applied post hoc, 24 of them (15 VAEs) do. The 41 have certified intervals for prior agreement with lower ends between 0.24 and 0.65, so the width criterion does not by itself give a high lower bound, and the label criterion is a threshold on label accuracy, not a test of downstream use. For these configurations direct measurement of prior agreement was cheaper and tighter than the certificate, and the paper says so. Certification adds something in two cases: on the gap side, where the target is agreement under the exact posterior, which cannot be sampled directly; and as a statement made in advance, since the dataset floor identifies 66 configurations in which no rate-side certificate can exist.

Corrections that affect numbers. (i) The submission called 131 scaled-grid configurations "certified". That count is the registered width test at the point estimate of agreement, which carries no confidence statement for the estimate; under the protocol's band, which accounts for its confidence interval, the count is 130. Both are now reported and named differently. (ii) The count of 240 "models" is 240 configurations from 204 distinct VAEs. (iii) Theorem 1(I') counted the degree of its moment threshold imprecisely; the statement is corrected (all moments of total degree at most m coincide, and a moment of total degree m+1 separates the pair). (iv) The Fano values reported for Theorem 3(d) are plug-in estimates and are now labeled as such.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the revision

We thank the reviewers. The revised PDF makes the changes below. No VAE was trained for the revision. Two analyses of the saved checkpoints were added, each with its criteria fixed before its full run (for the map audit, after its band widths had been seen; Appendices D.7 and D.9 list what had been seen in each case); they are marked as post-submission in Table 1, Sections 6.3–6.4 and those appendices. The main text is 10 pages.

  1. Model class and readouts (2Ds6, DtHP). The abstract and introduction state that the latent is continuous and that two code maps are applied after training. Section 2 defines by formulas the two readouts of the VAE experiments: centers fitted to encoder means, the most probable component or nearest center on the latent side, and the nearest decoded center on the output side.
  2. A result for linked readouts (DtHP, 2Egu Q1). Theorem 1 has a new Part (III): for an idealized k-means form of these shared-prototype readouts (globally optimal centers, a deterministic decoder), rebuilt for each model, two models with exact inference and a generative law equal to the data law match on items (m1)–(m6) of Definition 1 and have agreement 1−1/n and 1/n (Appendix A.7, with a verification script in exact arithmetic).
  3. Scope of Part (I). Its two maps are fixed and independent of the model, and its pair is not well specified; both facts are now stated (Sections 2–4, Appendices A.1 and A.3, Table 2).
  4. When drift can occur (2Egu Q4). New Corollary 1: the divergence between agreement on encoded data and under the prior is at most the model's misfit to the data plus its variational gap, so a well-specified model with exact inference has none.
  5. Map dependence and informative codes (2Egu Q3, Q5). Appendix D.7 reports the rate-side analysis under all four declared maps. Under the declared map no configuration meets both the width criterion and that audit's label-information criterion; under k-means 41 configurations (24 distinct VAEs) do, 24 of them under the stricter bar of the grid's original precommit, applied post hoc.
  6. A downstream interface (2Egu Q2, 2Ds6). Section 6.4 and Appendix D.9: in code-addressed generation, samples whose code is read back by the decoder-side map are classified as requested far more often than the rest on FashionMNIST and MNIST; the registered reading is negative on SVHN and CIFAR-10. Proposition 3 relates task error to how often the read code differs from the written one.
  7. Corrections.
    • The 131 scaled-grid "certificates" are width tests at the point estimate of agreement; under the protocol's band the count is 130. The two are now named and reported separately (Table 1, Sections 5.2 and 6.3, Appendix D.4).
    • The comparison reported as "72/72" in Appendix D.3 (now D.4) used two different judges on the same samples and does not show a routing benefit; that reading is withdrawn.
    • Theorem 1(I') counted the degree of its moment threshold imprecisely; the statement and proof are corrected.
    • "A rate budget is a functional of q̄ alone" was wrong; the budget depends on the encoder, the data law and the prior, and not on the code maps.
    • The Fano values for Theorem 3(d) are plug-in estimates and are labeled as such.
    • 240 "models" are 240 configurations from 204 distinct VAEs.
    • On six FashionMNIST models the floor is tight to within 0.03 nats, not 0.01; the 0.01 held only for a clipped mean.
    • Statements changed: Theorem 3(d) defines α as the accuracy of a fixed label map on the sampled code under the law that defines the rate; Theorem 3(e) is stated for rate-side budgets; Lemma 1 covers a ∈ [0,1], and Lemma 5 clips C_q to [0,1].
  8. Claims reduced to what is shown. "No item … can reveal" is now "does not determine"; "trained models behave as the theory predicts", "best previously available" and "standard diagnostics all sit inside Definition 1" are removed or made specific. The Shannon sentence and the historical framing are removed.
  9. Credit. The rate-side bound, Theorem 2(b), was suggested by an anonymous reviewer of an earlier submission of this work; the text no longer calls it new.
  10. Negative results kept. The preregistered replication (0/4), the registered generation analysis, the stricter PPCA gate and the two negative datasets of the new read-back analysis are reported in Table 1; the conclusion states the first two and the last.
  11. Figures. Figure 1 is redrawn to show the path used in the experiments. The labels of Figure 2 are corrected: panel (c) counts configurations and marks the width test.
  12. Supplementary material. The archive is updated with the precommits, hash records, scripts, logs and result tables of the two post-submission analyses, the exact-arithmetic check of Theorem 1(III), and the revised number checker.

Not changed: Theorem 2, Theorem 3(a) and, except for wording, 3(b); the preregistered verdicts and counts.

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

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