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Under review as a conference paper at ICLR 2027

Understanding the Predictive-State Bottlenecks of Transformer Models

Abstract

Sequence-prediction tasks typically require compressing an observation history into a compact internal state, making the state's dimensionality and organization central to neural model capacity. We study whether the residual width required for accurate prediction is governed by the latent-state count, the full posterior dimension, or the intrinsic dimension of the predictive state, using Transformers trained on hidden Markov processes. Across controlled families that separate these quantities, the width transition tracks predictive-state rank. Exact filtering constructions and bottleneck results connect this transition to the geometry of predictive representations, while readout and architectural controls distinguish state capacity from output parameterization. Also, we observe that the training is spectrally ordered, and a probe-calibrated analysis reveals a width-dependent mechanism: successive Transformer blocks increasingly favor high-variance belief directions; below rank, this becomes suppression of low-variance modes beyond an equal-treatment probe null, while sufficiently wide, adequately fitted models reverse the bias. Causal interventions separately show that the represented belief subspace contributes to prediction. In the tested contractive regime, filtering is strongly width-sensitive and only weakly depth-sensitive.

Primary area:
learning on time series and dynamical systems
Keywords:
predictive-state rank, hidden Markov models, Transformers, belief-state tracking, Bayes-optimal prediction, learning theory

Reviews

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

The research question is to quantify how large a width is required for the transformer to perform prediction. The authors use predictive-state rank, which is essential for prediction in linear state representation as Hankel rank, discriminated from hidden-state count or belief dimension. The sweep experiments and theoretical analysis demonstrate that predictive-state rank exhibits many important width transitions, even when the hidden-state count or belief dimension remains the same.

Critical strengths

The research direction is interesting to the research community because Transformers are widely used. Its understanding through width perspective in predictive state is worthy of being investigated.

Critical weaknesses
  • The results in Table 9 rather indicate that output-side architecture such as smaller width significantly affects the performance, rather than the internal predictive state. The current ablation study, such as Table 8, still does not close this issue.
  • What would be fundamentally “width” in a transformer? I mean, there are several dimensions, such as each in-out dimension in QKV and MLP. The controlled experiments on 256 width are performed, but this is still not convincing enough to clearly show the effect of width.
  • The width itself is also entangled with several factors, such as gradient dynamics and the optimizer. In other words, a thin model may be affected by several factors, such as the state information in the representation perspective, as the paper claims, different gradient dynamics, different numbers of parameters, and FLOPs.
  • The author says dim span{b_t}=K=128, which would not be achieved: under stationary distribution where macro state and clone identity are independent, we have dim span{b_t} \leq g=16.
  • Strictly speaking, the second-moment eigenvalue is different from variance. The used C is not covariance; rather, it is an uncentered second moment matrix.
  • Line 751-752 (leading eigenvectors): this would be false. After computing the eigenvector, \Sigma^{1/2} should be multiplied.
  • Writing should be improved:
    • “Equation equation 2”
    • “the readout is bias-free, all other linears carry bias.”
    • “Belief R^2, state accuracy, and per-mode R^2 are ridge probes” → they are not ridge probes themselves.
    • “stated threshold” → ?
    • “trivially predictable” → some explanation is required.
    • “several known HMMs of known predictive rank”
    • Incorrect pages for reference “Value-directed compression of POMDPs”
    • Incorrect issues for reference “Computational mechanics: Pattern and prediction, structure and simplicity”
Questions for authors

See the weakness above. Overall, I acknowledge that the authors performed several controlled ablation experiments to address my questions in advance; nevertheless, the current results are still not convincing enough to disentangle the effect of width from compound dynamics. Several measurements also depend on incorrect assumptions.

8 comments

Thank you for the detailed and insightful review. We addressed the architectural questions with more than 100 new runs and corrected the mathematical definitions and references.

W1: output architecture (Tables 8 and 9). We extended Table 9's configuration across residual widths, fixed attention width, and compared linear and MLP readouts with and without final LayerNorm. MLP readouts reduce excess loss by 11–40% relative to linear readouts, while all variants retain a broad transition near rr, with plateau onsets at d=18–24d = 18\text{–}24 (Fig. 1b, c; App. A.16). At fixed KK, the transition moves from d≈19d \approx 19 at r=16r = 16 to d≈30d \approx 30 at r=32r = 32. These sweeps show that the transition persists across readout choices, extending the exact-state calibration and output-only oracle.

W2: the definition of width. Width means residual dimension dd. Attention width also scaled with dd in the submission. It is now fixed at 64 (four heads of 16), with MLP width fixed at 256. Allowing attention width to scale with dd raises the d=8d = 8 gap from 0.062 to 0.105 bits and changes the d=16d = 16 gap by about 0.002 bits. The fixed-width controls remove the attention-width confound; a substantial residual-width deficit remains.

W3: optimization, parameters, and FLOPs. We added three controlled experiments (App. Table 12):

  • Parameters and compute: widening the d=8d = 8 model's MLP to match the parameter count of d=16d = 16 leaves its excess loss 4.1× higher. Dense FLOPs differ by 1.4%, and attention-score operations are identical.
  • Training budget: doubling the number of steps reduces the d=8d = 8 gap by 5–8% and produces essentially no improvement at d=16d = 16.
  • Data: increasing the dataset fourfold reduces the d=r/2d = r/2 gap by 1–4%, compared with 55–58% at d=2rd = 2r.

The narrow-model deficit persists under these controls, supporting a residual-capacity limitation in this regime. The learning rate was not tuned per width; we note this as a limitation (§7).

W4: belief span under stationarity. You are correct. In the identity-clone realization, every stationary joint law makes clone and macro independent, bounding the belief span by gg. We constructed a stationary-latent realization of the same token process with a large belief–rank separation. The original macro chain starts at stationarity, but clone identity is correlated with the initial macro state. The token process is stationary, while the joint latent initialization is not. We now distinguish posterior span 128 from predictive-belief span 120, and Hankel rank r=15r = 15 from full-state future-test rank q=16q = 16 (§2.1, App. A.19).

The new realization resamples clone identity from a macro-dependent distribution. At η=0.5\eta = 0.5, the predictive-belief span is 120 (119 centered), the posterior span is 128 (127 centered), and Hankel rank remains 15. Its non-predictive component carries 6–8% of centered variance (App. A.19). Per-token Bayes losses on the existing tokens agree to 10−910^{-9} bits, so the trained models and Table 1 prediction losses apply to this realization too.

W5: second moment versus variance. We have recomputed the per-mode analysis using Σ=Cov⁡(bt)\Sigma = \operatorname{Cov}(b_t), including the matched null and sensitivity covariate. We explicitly distinguish this covariance from the uncentered second moment C=E[btbt⊤]C = \mathbb{E}[b_t b_t^\top]. The occupancy-versus-Fisher comparison retains a 2–32% occupancy-truncation penalty over d=1–13d = 1\text{–}13 (App. A.4). The second moment is explicitly identified where used for homogeneous-span calculations and earlier results.

W6: Fisher-optimal subspace (lines 751–752). We corrected the missing transformation (App. A.3, A.15). If uiu_i is a leading eigenvector of Σ1/2GΣ1/2\Sigma^{1/2} G \Sigma^{1/2}, the encoder direction is (Σ+)1/2ui(\Sigma^+)^{1/2} u_i and the reconstruction subspace is span⁡(Σ1/2ui)\operatorname{span}(\Sigma^{1/2} u_i). The code used these encoder directions and optimal linear reconstruction, so the numerical values are unaffected.

W7: writing and references. We corrected the duplicated “Equation,” clarified the submitted architecture's bias terms, and described the quantities as “measured with ridge-regression probes.” The resolved-mode threshold is final R2≥0.1R^2 \ge 0.1. The text now explains why uniform generators and fixed reset positions need no state tracking, and refers to “HMMs whose predictive rank is known exactly.” Reference details are corrected to Poupart & Boutilier, pp. 1547–1554, and Shalizi & Crutchfield, 104(3–4).

We also corrected the stated ridge penalty to 1.0 and recomputed the g−1g - 1 projected-recursion column (now Table 8) with a converged occupancy estimate.

Revisions are marked in blue in the PDF. Submitted Tables 6, 7, 8, 9 are now Tables 8, 9, 10, 15.

Thank you for the substantial revision and additional experiments. The mathematical corrections, clearer definitions, and new architectural controls have addressed most of my earlier concerns. However, a few important issues remain:

  • The experiments still do not clearly distinguish predictive rank from the minimum number of HMM states needed for the same observations.
  • The loss decreases gradually around (d=r), and the new scaling experiments do not meet the authors' own predefined criterion.
  • The results may still be affected by incomplete training, so it remains unclear whether the observed performance differences are truly caused by limited representation capacity.

Thank you for the careful follow-up, and for acknowledging that the corrections and controls addressed most of your earlier concerns. We appreciate the remaining points and have run additional experiments to address them, as described below. All of these results are included in thelatest version.

1. Predictive rank versus minimal state count. Thank you for highlighting this distinction. We agree that, in our families, predictive rank and minimal state count coincide, and we state the claim at exactly that level in the abstract and introduction. What our experiments do establish is that the width transition reflects the observable process rather than how it is realized: splitting each state into clones, or adding 112 belief directions that never affect predictions, leaves the transition unchanged, while raising the predictive rank moves it.

2. Gradual decrease and scaling. We agree that the transition is broad, and we describe it as such rather than as a threshold. To examine scaling more closely, we ran an additional rank, r=8r = 8, and measured how wide a model must be to reach a given accuracy. That width doubles each time the predictive rank doubles: 6.3, 12.0, and 24.0 at r=8,16,32r = 8, 16, 32 for the same excess loss of 0.015 bits, with the same scaling from 0.015 to 0.020 bits. We do not claim an exact collapse of the full loss curve, since that would also require the plateaus to scale. At a fixed data budget, the plateaus are set by data rather than width: fourfold more data lowers the 2r2r gap by 55–58% but the r/2r/2 gap by only 1–4% (App. Table 12).

3. Training versus capacity. This is an important question, and we tested it directly. If narrow models were simply undertrained, giving each width its own best learning rate should close most of the gap. We tuned the learning rate separately below, at, and above rank (10−410^{-4} to 10−210^{-2}, two seeds). Narrow models do prefer larger rates (10−210^{-2} at d=8d = 8 versus 10−410^{-4} at d=32d = 32), and tuning helps them most: 25% lower loss at d=8d = 8, compared with 9% at d=16d = 16 and 7% at d=32d = 32. Even so, the below-rank model retains 3.5–3.7× the loss of the at-rank model, so tuning closes only about a fifth of the gap. Doubling the training steps and matching parameter counts also leave the gap in place (App. Table 12). We therefore believe that, in this regime, the below-rank deficit reflects limited width rather than optimization.

These results are added to §4.3 and Appendices A.16 and A.17. Thank you again for your thoughtful comments, which have helped us make the paper's claims more precise.

Reviewer_N6NPOpenReview ↗
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Paper summary

The paper asks what determines the residual width a transformer needs to predict sequences generated by hidden Markov models (HMMs). The three candidates are the number of latent states, the full belief (posterior) dimension, and the predictive-state rank, meaning the dimension of the smallest state that is enough to predict the future. The authors build synthetic HMM families, such as “ring” and “clone” processes, designed to separate these three quantities. They report that the width at which loss approaches the Bayes-optimal value tracks predictive-state rank. Exact filtering constructions, bottleneck results, and readout/architecture controls are used to support this.

Critical strengths

-- HMMs give known optimal beliefs and an optimal loss, so the learned representations can be checked against the truth rather than guessed. This makes the measurements trustworthy, and the reported results appear correct and internally consistent.

-- Separating state count, belief dimension, and predictive rank is a useful way to frame the problem. The authors openly report their own ablations (Table 9) and their comparison of importance and variance directions. The width-dependent reversal of learning order is an interesting observation in its own right.

Critical weaknesses
  1. The evidence for "width tracks predictive-state rank" does not isolate predictive rank (Fig. 1, Table 1, Sec. 4.1, Table 9).

    • The ring vs. clone comparison matches by construction. The comparison is clone (K=128K=128, g=16g=16) against ring (K=16K=16, r=16r=16). In the clone process, the copies of a state cannot be told apart from the observations, so it is effectively a 16-state process. Both processes therefore also have the same effective number of states, and the match with rr is expected by construction.
    • The clone spectra scaling is arithmetic. The spectra shrinking by the clone factor cc follows directly from splitting belief mass evenly over cc copies. It is not a property the transformer learned.
    • The plateau is not shown to be a width limit. Section 4.1 reads the loss plateau as rr increases as a width limit. However, the models are not near the Bayes-optimal loss. Table 9 also shows that untying the input/output embeddings, adding an output bias, and fixing the hidden-layer sizes lower this loss at the same width. The authors present these as controls that separate state capacity from output parameterization. But if output parameterization alone moves the plateau, the Sec. 4.1 plateau cannot be read as a width limit.

    This matters for my assessment as this is the paper's main claim.

  2. The variance-ordering result depends on how β\beta is defined (learning-order analysis). β\beta measures selectivity by variance only. A direction can have high variance and matter little for prediction, and the reverse is also possible. The authors themselves find that importance and variance directions differ, yet the β\beta and probing analysis use variance only. "Learned from high to low variance" may therefore partly reflect the choice of metric rather than how the model actually learns.

Questions for authors

Clarifications (these could change my score):

  1. Is the clone process (K=128K=128, g=16g=16) observationally equivalent to a 16-state process? If yes, how does the ring vs. clone comparison separate predictive rank from the minimal number of states?
  2. In Table 1, do the ring and clone processes generate the same symbol distribution? If they do, why do their losses differ?
  3. Given that the Table 9 changes lower the loss at fixed width, why is the Sec. 4.1 plateau attributed to width rather than to output parameterization?
  4. Since you find that importance and variance directions differ, why does β\beta use variance only? Does the learning order change if directions are ranked by importance?

Addionally,

  • A comparison in which predictive rank and the minimal number of states genuinely differ.
  • The width sweep re-run under the Table 9 configuration, reporting the gap to the Bayes-optimal loss.
  • An importance-aware version of the learning-order analysis.
5 comments

Thank you for the detailed review. We addressed width and learning order with over 100 new runs and probe-calibrated analyses.

W1a, Q1: ring–clone equivalence. The g=16g = 16 clone process is observationally equivalent to a 16-state process. The corpora share token streams, hence identical width curves. We now use this as a realization-invariance check (§4.3, App. A.18). The width evidence comes from controlled sweeps at two predictive ranks with the same generating-state count K=128K = 128.

W1b: clone spectra. We have made the 1/c1/c scaling from splitting belief mass over cc copies explicit and moved the panel to App. A.18 as a check that state splitting preserves occupancy rank.

W1c, Q3, request (b): width versus readout. We reran Table 9's configuration with attention width fixed at 64, MLP width at 256, untied embeddings, and a readout bias. Checkpoints use a separate validation split; training sets are 4–8× larger in tokens. Test excess loss is expected KL⁡(pBayes∥pmodel)\operatorname{KL}(p_{\mathrm{Bayes}}\Vert p_{\mathrm{model}}) (Fig. 1; App. A.16).

  • At r=16r = 16, MLP–LayerNorm reaches 0.0076 bits/token at d=16d = 16 and 0.0045 at d=24d = 24 (App. Table 11).
  • Of the log excess-loss reduction from d=r/2d = r/2 to 2r2r, 75% is achieved by d=rd = r (App. A.17); 90% of the observed improvement is reached by d≈1.2rd \approx 1.2r (§4.3).
  • MLP readouts reduce excess loss by 11–40% relative to linear readouts. Both, with or without final LayerNorm, retain a broad transition near rr, with plateau onsets at d=18–24d = 18\text{–}24.
  • Fourfold more data reduces the gap by 1–4% at d=r/2d = r/2, versus 55–58% at d=2rd = 2r: the narrow-model deficit persists while the wider-model plateau improves.
  • At fixed K=128K = 128, raising rank from 16 to 32 shifts the transition from d≈19d \approx 19 to 3030. The stricter pre-registered proportional-scaling criterion is not met (App. A.17).

These controls distinguish the persistent narrow-model deficit from improvements due to readout choice and more data.

W2, Q4, request (c): variance versus importance. We now separate probe-induced ordering from learned allocation and timing. An equal-treatment schedule already produces variance-ordered acquisition, so order alone is not the evidence. In the centered covariance basis, we fit log-odds decodability jointly against log variance and log one-step Fisher sensitivity (importance per unit displacement), using the same probe for data and nulls. Across 16 runs (two readouts, four widths, two seeds):

  • The variance coefficient exceeds the matched null by +0.85 to +2.48 at d=r/2d = r/2 and +0.18 to +0.37 at d=rd = r, and falls below it above rank (−0.10 to −0.19), in every run.
  • Variance selectivity exceeds the null from steps 650–900, under 1% of training, at every width and seed.
  • To distinguish timing from final allocation, we also match each mode's final decodability in a shared-schedule null. The t90t_{90} exponent remains higher by 3.1–4.1 at d=r/2d = r/2 and 0.5–0.9 at d=rd = r. Above rank it is higher for MLP readouts (0.5–0.7) and lower by 0.20–0.35 for linear readouts. Both seeds agree in sign in every cell.
  • Variance explains 71–99% of per-mode log-odds variation. Sensitivity contributes positively on both seeds in six of eight settings, explains up to 22% of the remainder, and adds at most 0.03 to total regression R2R^2. Its coefficient decreases through depth in 14 of 16 runs.
  • Given variance rank, the partial rank correlation of t90t_{90} with sensitivity rank is −0.36 to +0.47 (mean +0.06): no consistent additional timing association. Rank 1 denotes highest variance or sensitivity and earliest acquisition. Its marginal association at d≥rd \ge r is close to the null, consistent with variance–sensitivity correlation 0.74.

The offsets, their early onset, and allocation-matched timing show mode-specific allocation and timing beyond the probe. Importance adds little beyond variance: it contributes modestly to final decodability, with no consistent additional association with acquisition time (§3.6, §4.4, App. A.4; App. Fig. 5).

Q2: the same symbol distribution in Table 1? Table 1 uses the separate rank–span process, with its own macro transition matrix and shorter sequences (128 versus 256 tokens), so its losses need not match the ring's. We distinguish Hankel rank r=15r = 15 from full-state future-test rank q=16q = 16. Every width uses the same data. Ring and mixing-clone losses agree at every width and seed.

Request (a): rank versus minimal HMM state count. In the ring and mixing-clone corpora, rr equals the minimal HMM state count (App. A.2), so these sweeps do not separate the two. We identify this separation as an open test in §7. For the rank–span process, the bounds 15≤Kmin⁡≤1615 \le K_{\min} \le 16 still allow Kmin⁡=r=15K_{\min} = r = 15.

Revisions are marked in blue in the PDF. Submitted Tables 6, 7, 8, 9 are now Tables 8, 9, 10, 15.

Reviewer_N6NPOpenReview ↗

Thanks for response but main concern stays

Thank you for the response and the new experiments. They resolve W1b, W1c and W2. However, the main concern, which is directly related to papers main contribution stays as it is:

The paper claim is that width tracks predictive rank and not state count. The response to (a) confirms that in every corpus you tested, r equals the minimal number of HMM states, so the experiments cannot tell the two apart. The only state count paper separate from r is the size of a non-minimal realization, and a model trained on tokens must ignore that by construction. Therefore, as per my understanding, moving the r versus K_min question to Section 7 removes the one test that would support the paper's main contribution. Meanwhile title, abstract and intro still claim it.

I feel paper has marit but needs complete scoping, which is beyond the review cycle scope.

Thank you for the follow-up. We are glad the new experiments resolve W1b, W1c, and W2.

Main contribution and scope. We agree with your reading. In every corpus we tested, rr equals the minimal number of HMM states, and the non-minimal realizations are controls that a token-trained model must ignore by construction. The paper should therefore not claim to distinguish predictive rank from minimal state count, and we rescope the abstract, introduction, and contribution statement so that they do not.

We would respectfully note that this is a change of framing rather than of results, and that it can be made within this cycle. The revised statements are:

  • Abstract: "We study how residual width constrains this state in Transformers trained on hidden Markov processes whose beliefs, predictive rank, and Bayes-optimal loss are known exactly. In controlled sweeps at a fixed generating-state count, the width transition moves with predictive-state rank and is unaffected by state splitting or by non-predictive posterior dimensions; in these families, predictive rank also equals the minimal HMM state count."
  • Contribution 1: "At a fixed generating-state count, the width transition moves with predictive rank, and realization-invariance controls show that state splitting and non-predictive posterior directions leave it unchanged. In these corpora, rr also equals the minimal HMM state count."
  • §4.3 heading: "The width transition moves with predictive rank and is realization-invariant."

Under this scope, the main results stand on their own. With an additional rank (r=8r = 8), the width needed to reach a given accuracy doubles each time the predictive rank doubles: 6.3, 12.0, and 24.0 at r=8,16,32r = 8, 16, 32 for an excess loss of 0.015 bits. A per-width learning-rate sweep leaves the below-rank deficit at 3.5–3.7×. The width-dependent reversal you noted is a property of the learned representations that observational equivalence does not determine. Below rank, the Transformer blocks build a preference for high-variance belief directions beyond an equal-treatment probe null, and above rank this preference reverses.

The title refers to the predictive state as the object of study and does not assert predictive rank over minimal state count. We would be glad to adjust it if you or the AC prefer.

Thank you again for your careful reading, which has helped us state the paper's contribution more precisely.

Comments on the paper

3 comments

Thank you for the thoughtful review. We now report the requested dense width sweep, a second predictive rank at fixed K=128K = 128, and separate validation and test results.

Main weakness: the separation holds largely by construction. The revision separates realization-invariance controls from the learned width transition (§4.3). Observational equivalence explains the ring–clone comparison, and the rank–span process gives no prediction incentive to retain clone identity. The new sweeps hold attention and MLP widths fixed, use untied embeddings and a readout bias, and increase training data by 4–8×. At fixed K=128K = 128, the width reaching 90% of the observed improvement moves from d≈19d \approx 19 at r=16r = 16 to d≈30d \approx 30 at r=32r = 32. This rank-dependent shift does not meet the stronger pre-registered proportional-scaling criterion (App. A.17).

Across the 16 controlled runs, the matched-null analysis shows that variance selectivity appears within the first 1% of training, develops through the Transformer blocks, is strongest below rank, and reverses above rank in adequately fitted models. These are properties of the learned representations that observational equivalence alone does not predict (§4.4, §4.6, App. A.4).

The allocation result also holds below rank at g=32g = 32, where the variance-slope offset is +0.82 to +0.86. Relative to the null, the highest-variance quartile is decoded 1.5 log-odds units better and the lowest 0.5 worse, although variance spans 13× across these quartiles and oracle discard cost spans only 2.1× (§4.7, App. A.3).

Linear rank rr versus intrinsic dimension r−1r - 1. In the controlled r=16r = 16 and r=32r = 32 corpora, the Hankel rank is rr, the affine predictive dimension is r−1r - 1, and the full-state future-test rank satisfies q=rq = r (App. A.2). The new dense grid tests the transition within these families. At r=16r = 16, excess loss falls by 13.7%, 13.6%, and 14.5% per added width from d=14d = 14 to 17, with no break at 15 or 16. In this revision, we stated this scope explicitly. The dense grid locates the transition within these families, which separates linear rank from a substantially smaller intrinsic dimension requires a different experiment (App. A.12, §7).

Theory. We now state the theorem's scope explicitly. Theorem 1 applies invariance of domain to continuous single-vector predictive bottlenecks; an affine filter attains the bound. It does not impose the same bound on a Transformer using distributed prefix memory (§2.2).

Q1: a dense grid with per-seed spread. At r=16r = 16, the MLP readout with final LayerNorm was run at d=8,14,15,16,17,18,20,24,32d = 8, 14, 15, 16, 17, 18, 20, 24, 32. The corresponding no-final-LayerNorm comparison covers d=14–18,20,24,32d = 14\text{–}18, 20, 24, 32, and the linear readouts were run at d=16,18,24,32d = 16, 18, 24, 32, with two seeds per reported cell (App. Table 11). We report individual-seed ranges; the maximum spread is 1.6×10−31.6 \times 10^{-3} bits. The decline is smooth through 15 and 16, where 75% of the reduction in log excess loss from r/2r/2 to 2r2r is achieved by d=rd = r, and each readout variant is within 1.25× of its own plateau by d=18–24d = 18\text{–}24. These measurements locate a broad transition near rr without identifying a sharp threshold at rr or r−1r - 1.

Q2: selection and reporting. All new controlled sweeps now separate selection from reporting. Checkpoints are selected on validation data and evaluated on an independent test split. The original phrase meant the mean of each seed's minimum loss over training, using the same held-out set for selection and reporting. The rank–span results in Table 1 retain that original protocol. Re-evaluating the earlier cells under validation selection changed the reported gaps by less than 10−310^{-3} bits. We also increased the training datasets, which substantially reduces the data limitation seen at larger widths in the earlier sweeps (App. A.18).

In Table 5, we recomputed the occupancy-versus-Fisher comparison on centered covariance, which gives an occupancy-truncation penalty of 2–32% over d=1–13d = 1\text{–}13. The penalty persists at widths that retain near-degenerate eigenvalue pairs together (App. A.4). The rotation-symmetric band rings remain the control in which the two orderings coincide (§4.7, App. A.3).

Revisions are marked in blue in the PDF. Submitted Tables 6, 7, 8, 9 are now Tables 8, 9, 10, 15.

Reviewer_8fk4OpenReview ↗

Response to rebuttal

Hi Authors,

Thank you for the response. All my concerns have been addressed, I will keep my score as weak acceptance.

AuthorsOpenReview ↗

Summary of the rebuttal and revisions

We thank the AC and the three reviewers for a detailed and constructive discussion. 8fk4 recognized the pre-specified oracle criterion and the allocation results, N6NP confirmed that W1b, W1c and W2 are resolved, and nVWm noted that the paper has improved considerably. Below we summarize the main concerns and the added evidence (changes in blue in the revised PDF). Analysis rules for new experiments were fixed and hashed before training; post hoc analyses are labelled.

Claim. In Transformers trained on HMMs with exactly known beliefs, the location of the width transition follows predictive (Hankel) rank rr. At a fixed generating-state count K=128K=128, the width reaching an excess loss of 0.015 bits doubles with each doubling of rr (dτ=6.3d_\tau=6.3, 12.0, 24.0 at r=8r=8, 16, 32). It is unchanged by state splitting, by 112 non-predictive posterior directions, and by raising the minimal HMM state count at fixed rr. We do not claim that the full loss curves scale proportionally.

1. Predictive rank vs. minimal state count (N6NP, request (a); nVWm, point 1). We built a family in which the two differ: a shifted band-limited ring with r=2b+1r=2b+1, for which we prove that every HMM realization has at least nn states (App. A.21, 76 runs). At r=9r=9, raising nn from 32 to 256 (Kmin⁡≥28rK_{\min}\ge 28r) changes dτd_\tau by at most 6%, and the excess loss at every width by at most 1.23×, with no consistent direction in nn. Raising rr from 9 to 17 multiplies the excess loss by 2.8–4.5× and dτd_\tau by 1.5–2.0. This comparison has no free parameter, so the conclusion does not hinge on the post hoc dτd_\tau thresholds.

2. Width vs. readout, attention, parameters and data (N6NP, W1c; nVWm, W1–W3). A controlled configuration fixes attention and MLP width at every residual width and unties the readout. Readout and normalization variants change the level of the curve, but each shows a broad transition near rr (Fig. 1). A d=8d=8 model at the parameter count of d=16d=16 (FLOPs within 1.4%) remains 4.1× worse, and fourfold more data changes the d=r/2d=r/2 gap by 1–4% but the d=2rd=2r gap by 55–58% (App. A.16, Table 12).

3. Optimization vs. capacity (nVWm, point 3). Tuning the learning rate per width (10−410^{-4} to 3×10−23\times10^{-2}; 10−210^{-2} is an interior optimum at d=8d=8) closes only 11–14% of the log-gap between d=8d=8 and d=16d=16. With each width at its best rate, G(8)/G(16)G(8)/G(16) is 3.9 at 1.5×1051.5\times10^5 steps and 3.6 at 3×1053\times10^5, above the pre-registered 2.5. A pre-registered token-matched run (batch 1024, the tokens of 1.2×1061.2\times10^6 steps; one seed) gives 3.4, inside the projected 2.7–3.6: four times the training tokens lower the excess loss by only 9% at d=8d=8 and 3% at d=16d=16. At r=32r=32, doubling the steps lowers the excess loss by 9% at r/2r/2, changes it by at most 5% at rr and 2r2r, and moves dτd_\tau by at most 6% (App. A.16, A.17). These controls bound, rather than exclude, an optimization contribution.

4. Scaling (nVWm, point 2). The claim concerns the location of the transition. The normalized dτd_\tau ratios are 0.88–1.00 for every rank pair, seed and threshold from 0.015 to 0.020 bits (App. A.17). As a check on the theory, a belief-bottleneck oracle, which involves no Transformer training, places its knee at 1.19r1.19r, 1.08r1.08r and 0.99r0.99r and meets the proportionality criterion fixed before it was run (App. A.22). The stricter full-curve criterion of Table 13 is not met, so we do not claim proportional collapse.

5. Variance vs. importance (N6NP, W2 and request (c); nVWm, W5). The per-mode analysis now uses the centered covariance, a matched equal-treatment probe null, and one-step importance as a joint covariate (§4.4, §4.6, App. A.4). Below rank, variance selectivity exceeds the null in every run (+0.85 to +2.48 at d=r/2d=r/2); it weakens with width and reverses above rank. Importance explains at most 22% of the per-mode variation beyond variance, and mode-specific acquisition timing remains after matching each mode's final decodability.

6. Dense grid, selection, rr vs. r−1r-1, theory (8fk4). A dense grid at r=16r=16 (d=8d=8, 14–18, 20, 24, 32; two seeds; Table 11) shows a smooth decline through d=15d=15 and 16, so the transition lies near rr rather than at a sharp knee. New sweeps select checkpoints on a validation split. The grid does not separate rr from r−1r-1; we state this and list it as a next step (§7). Theorem 1 is presented as an attained bound for single-vector bottlenecks (§2).

7. Technical corrections (nVWm, W4–W7). We added a stationary-latent realization of the rank–span corpus (App. A.19), corrected the Σ1/2\Sigma^{1/2} statement (computations unaffected), and fixed the writing and references.

Thank you again for all the time reviewers and AC contributed, and the valuable suggestions to this work.

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

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