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Under review as a conference paper at ICLR 2027

Codes for Representation, Items for Prediction: Rethinking the Learning Interface of Semantic-ID Recommendation

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Abstract

Semantic IDs (SIDs) represent items through compositions of shared discrete codes, yet generative recommenders typically also use these codes as autoregressive prediction targets. We observe that, under the same backbone configuration, direct item prediction can outperform autoregressive SID prediction, motivating the hypothesis that representation sharing and prediction factorization need not be coupled. To examine this hypothesis, we analyze what changes when a complete-item decision is factorized into an autoregressive SID path. At the distribution level, a locally normalized legal SID tree can represent any strictly positive catalog distribution, while controls over invalid-continuation competition do not explain the observed ranking gap. This directs attention to the supervision structure: under teacher forcing, SID prediction directly supervises branch logits along the target path, progressively refining nested target subtrees, whereas non-target subtrees compete through shared entry branches without direct supervision of their internal conditionals from the current example. Progressively controlled comparisons show that direct item scoring remains stronger under increasingly matched designs and exact catalog ranking. Based on this decoupling principle, we propose Next-item Representation Prediction (NRP), which composes shared SID embeddings into complete-item representations and directly optimizes item-level scores without an item-specific embedding table. Across three public datasets, NRP achieves competitive performance against strong sequential and generative baselines and improves transductive cold-start recommendation.

Primary area:
generative models
Keywords:
Sequential Recommendation, Generative Recommendation, Semantic IDs

Reviews

Among:
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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_AZT7OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper asks whether Semantic IDs should serve as both shared item representations and autoregressive prediction targets. It shows that an unrestricted legal SID tree can express any positive catalog distribution and contrasts the supervision applied to branch logits and complete-item scores. Based on this analysis, NRP builds item vectors from shared code embeddings and trains them with full-catalog item cross-entropy.

Critical strengths

The analysis separates distributional expressivity from the organization of supervision, which offers a useful perspective on SID-based recommendation.

Critical weaknesses

W1: The method is close to VQ-Rec and especially DiGR, which already combine SID-based item representations with item-level scoring. The paper discusses this overlap, but its distinction from DiGR is not sufficiently sharp, and no direct comparison is provided.

W2: The gradient analysis does not establish that the supervision structure is the main reason for the performance gap. The output heads and optimization paths still differ. Some main-table baselines also use published results from different pipelines, and the larger-catalog experiment reports only one seed.

Questions for authors

Q1: How does NRP compare with DiGR under matched SID construction, backbone, training budget and exact ranking? Which gains remain attributable to the proposed contribution?

Q2: Please provide more direct evidence to prove that the observed performance improvements are caused by the supervision structure rather than differences in the prediction heads or the optimization process.

4 comments
AuthorsOpenReview ↗

Response to Reviewer AZT7

Thank you for the constructive review and for recognizing the value of separating distributional expressivity from supervision organization. Below are our new results and planned revisions.

Q1. Comparison with DiGR and our contribution. We now report 5-seed reproductions of original DiGR and DiGR (GPT-2) (updating Table 1 and Table 6 in Appendix B.3). DiGR (GPT-2) shares NRP's GPT-2 architecture, fixed RQ-KMeans SIDs, exact full-catalog testing, and history filtering. NRP retains its original fixed configuration (20-250 epochs), while DiGR (GPT-2) independently searches 3 learning rates and 2 temperatures, with early-stopping patience 10 and no fixed epoch cap. NRP outperforms both DiGR versions on all reported metrics across all three datasets (e.g., Beauty 5-seed Recall@10 is 0.0928 for NRP vs. 0.0635 for DiGR, 0.0496 for DiGR (GPT-2), and 0.0798 for VQ-Rec (GPT-2)).

To examine the contribution of composition, we independently tuned all five composers (Table 22, Appendix D.4) over the same 3-by-3 learning-rate/temperature grid with catalog centering disabled. The strongest simple aggregator, Sum, achieves Beauty/Toys Recall@10 of 0.0508 / 0.0509, vs. 0.0944 / 0.0970 for the residual MLP (D=6D=6). The residual MLP remains substantially stronger after independent tuning with centering disabled, supporting this learnable composition design.

These results provide both end-to-end comparisons and evidence on the composition module. Relative to existing SID-based item scoring (Section 2 / Appendix B.4), our main contribution is systematic theoretical analysis and progressively controlled experiments supporting SID sharing with direct optimization of complete-item scores. We establish that a legal SID tree with unrestricted node conditionals has no inherent catalog-level expressivity limitation, and show that direct scoring remains stronger when we normalize over legal branches, progressively align history representations and model designs, and rank the full catalog exactly.

Q2. Direct evidence, optimization controls, and result reliability (W2). We added two controls addressing scoring-head differences and optimization, plus multi-seed evaluations for W2:

  1. Fixed-Head Objective Intervention (Table 2(e), Section 6.3 / Appendix C): Under the same full-vocabulary AR scoring architecture, SIDs, training events, and paired initialization, we compared standard NTP with catalog-normalized sequence-level training, Lcat-AR=−14log⁡qθ(c(i+)∣h)∑j∈Iqθ(c(j)∣h)\mathcal{L}_{\text{cat-AR}} = -\frac{1}{4}\log \frac{q_\theta(c(i^+)\vert h)}{\sum_{j \in \mathcal{I}} q_\theta(c(j)\vert h)}, using the same 1/4 loss scaling, independent equal-budget LR searches, and exact full-catalog validation/testing. Because the full-vocabulary scorer assigns probability outside I\mathcal{I}, catalog normalization introduces a nonconstant, parameter-dependent term into the objective that enforces catalog-wide competition without changing the AR scoring head:
Fixed AR Scorer (3 Seeds)Beauty R@10Beauty N@10Toys R@10Toys N@10
Standard NTP0.05910.03150.05390.0281
Catalog-Normalized AR0.0662 (+12.0%)0.0364 (+15.6%)0.0665 (+23.4%)0.0367 (+30.6%)

Our gradient analysis characterizes direct supervision at branch-logit and complete-item-score coordinates, and a single-step diagnostic (Appendix C) shows shared-parameter updates alter relative probabilities within non-target subtrees (0.0645 / 0.0669 on Beauty/Toys) as collateral drift. This fixed-architecture intervention directly links the catalog-level objective to improved ranking.

  1. Independent Optimization Tuning for Table 2(d) (Appendix C): We independently tuned the composed-history LegalCE, StandardCE, and NRP models over the same 5-point learning-rate grid {5e-5, 1e-4, 3e-4, 1e-3, 3e-3}, using exact full-catalog validation to select configurations (identical events, AdamW settings, and budgets of 20-400 epochs, patience 10; identical history centering and D6 composer):
Model (5-LR Grid, Exact Val/Test)Beauty N@10Toys N@10
Matched AR (StandardCE / LegalCE)0.03696 / 0.035720.03058 / 0.03087
NRP (Item CE)0.053680.05659
  1. Result Sources & Multi-Seed 64K-Catalog Evaluation (W2): We reproduced EAGER, COBRA, and DiffGRM under our common split and evaluation protocol; all Table 1 baselines will report 5-seed reproduced means, with published values listed separately as references in Table 6. On the larger CDs and Vinyl catalog (64,443 items, Table 27 in Appendix F), SASRec, RPG, and NRP now use 3 training seeds: Recall@10 (mean ±\pm std) is 0.0503±0.00210.0503 \pm 0.0021 for SASRec, 0.0431±0.00170.0431 \pm 0.0017 for RPG, and 0.0938±0.00180.0938 \pm 0.0018 for NRP, with NRP retaining the highest mean on all reported metrics.

Dear Reviewer AZT7,

With the discussion period ending in about two days, we wanted to briefly follow up and check whether our response and additional experiments have addressed your questions.

To directly resolve your concerns in W1/Q1 and W2/Q2, we have provided:

Matched 5-seed comparisons with DiGR and DiGR (GPT-2) alongside independent 3x3 learning-rate/temperature tuning across all five composers, isolating the substantial gain of learned nonlinear composition over simple pooling.

A fixed-architecture training-objective intervention (comparing standard NTP with catalog-normalized sequence training under the exact same AR head) and independent 5-point learning-rate sweeps for Table 2(d), directly demonstrating the benefit of catalog-level supervision (+15.6% / +30.6% NDCG@10) independent of prediction-head and optimization differences.

Unified 5-seed local reproductions for all baselines in Table 1 and 3-seed evaluations on the 64K-item CDs and Vinyl catalog.

We would be very grateful to hear if these results address your concerns, and we remain happy to clarify any further questions before the deadline. Thank you for your time and consideration!

Thank you for the authors’ response. The rebuttal addressed some of my concerns, and I will raise my rating.

We sincerely thank you for your time and for raising your rating. We are glad our response was helpful, and we will ensure that the matched DiGR comparisons, the fixed-architecture catalog-normalization intervention, and the multi-seed evaluations are all thoroughly incorporated into the final revision.

Reviewer_JWPKOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
3(+1)
Read review
Paper summary

The paper studies whether Semantic IDs need to serve as both item representations and autoregressive prediction targets. It proposes NRP, which composes shared code embeddings into item representations and scores complete items using a causal history encoder and an item-level cross-entropy objective. The analysis distinguishes catalog-level expressivity from the allocation of supervision under different prediction parameterizations. Experiments on Amazon recommendation datasets compare NRP with existing methods and progressively match history representations, model capacity, initialization, and ranking procedures. The paper also examines composition choices, cold-start recommendation, and inference efficiency.

Critical strengths
  1. The controlled comparisons are the strongest part of the paper. In particular, Table 2(d) aligns the composed-history design, backbone, composer, parameter budget, and initialization of shared components, and uses exact catalog ranking on both sides. NRP improves NDCG@10 from 0.0324 to 0.0538 on Beauty and from 0.0287 to 0.0561 on Toys. These are substantial differences, and the additional checks in Appendix C make it difficult to dismiss them as simply a beam-search or model-size effect.

  2. The theoretical discussion is careful about its scope. The paper does not confuse autoregressive factorization with a loss of catalog-level expressivity. Appendix A.4 acknowledges the effect of shared parameters, and Appendix A.6 gives a tree construction with the same loss and parameter gradients as item softmax. I appreciate these qualifications; they make the empirical question more precise and avoid claiming that one factorization must always be better.

Critical weaknesses
  1. The added contribution over the closest item-scoring work is not yet sufficiently established. As the authors acknowledge in Appendix B.4, DiGR already separates SID-based representation from token prediction and trains with item-level likelihoods. NRP's contribution therefore rests largely on its supervision analysis, controlled study, and composition design. However, there is no end-to-end DiGR comparison under the same protocol. The Mean variant in Table 19 is explicitly an internal aggregation control, so it does not establish the difference from a tuned DiGR implementation. I would find a clearer account of what the present study establishes beyond DiGR, and a focused comparison where feasible, more informative than additional comparisons with less closely related methods.

  2. The controlled gains are convincing as an empirical observation, but their interpretation still leaves two related questions.

First, the output-coordinate gradient analysis does not by itself show why the trained networks differ so much. Actual updates pass through shared parameters and depend on the prediction head and optimizer, as Appendix A.4 itself notes. The results support NRP over the tested AR implementations, but do not yet isolate the lack of direct supervision within non-target subtrees as the main explanation. This matters because the analysis is a central part of the contribution beyond prior item-scoring methods. I do not see this as an error in the derivation; I would like the connection between the analysis and the observed gains to be better supported or more narrowly stated.

Second, matching hyperparameters does not necessarily give both prediction heads an equally suitable optimization setting. The paper does not clearly report separate tuning for the composed-history AR model in Table 2(d); the learning-rate sweep in Appendix C.3 concerns a different AR configuration. The differences among Mean, Sum, and Scaled Sum in Table 19 also suggest that score scale and optimization deserve attention. This does not show that the comparison is unfair, but it leaves some uncertainty about how much of the gap remains after tuning the key matched models separately.

Questions for authors
  1. What do the authors see as the main new finding relative to DiGR? Is there a matched DiGR comparison available, or can the existing results clarify which part of NRP accounts for the improvement over prior code-based item scoring?

  2. Which existing result most directly links the ranking improvement to the proposed supervision-allocation explanation, rather than to the broader change in prediction-head parameterization? Clarifying the intended scope of this explanation would already be helpful; I am not asking for a general theorem of superiority.

  3. For Table 2(d), were learning rates selected separately for the two models? Please also clarify whether AR loss is averaged over tokens or summed per item, and whether the history-centering treatment is the same. If separate tuning results are already available, they would be useful. A small sensitivity check of this central comparison would be sufficient; I do not think a broad new experimental suite is needed.

3 comments
AuthorsOpenReview ↗

Response to Reviewer JWPK

Thank you for the thoughtful review and for highlighting our controlled comparisons and theoretical qualifications. Below are our new results.

Q1. New findings, matched DiGR comparison, and source of gains. While DiGR separates SID representation from token prediction, our main contribution is systematic theoretical analysis and progressively controlled evidence for retaining SID sharing while optimizing complete-item scores. We prove that a legal SID tree with unrestricted node conditionals has no inherent catalog-level expressivity limitation. Loss decomposition characterizes invalid-continuation competition, while gradient analysis contrasts target-path branch supervision with complete-item supervision. Direct scoring remains stronger when we normalize over legal branches, progressively align history representations and model designs, and rank the full catalog exactly (Table 2); thus, the gap cannot be explained solely by invalid continuations or approximate search.

We now report 5-seed reproductions of original DiGR and DiGR (GPT-2) (updating Table 1, Table 6, and Section 2 / Appendix B.4). DiGR (GPT-2) shares NRP's GPT-2 architecture, fixed RQ-KMeans SIDs, exact full-catalog testing, and history filtering; NRP retains its fixed configuration while DiGR (GPT-2) searches 3 learning rates and 2 temperatures. NRP outperforms both DiGR versions on all metrics across all three datasets (e.g., Beauty 5-seed Recall@10 is 0.0928 for NRP vs. 0.0635 for DiGR and 0.0496 for DiGR (GPT-2)).

To examine composition and the score-scale sensitivity among Mean, Scaled Sum, and Sum in Table 22, we independently tuned all five composers over the same 3-by-3 learning-rate/temperature grid with catalog centering disabled (Appendix D.4). The strongest simple aggregator, Sum, achieves Beauty/Toys Recall@10 of 0.0508 / 0.0509 vs. 0.0944 / 0.0970 for NRP's Residual MLP (D=6D=6), confirming the benefit of learned nonlinear composition.

Q2. Evidence and scope of the supervision explanation. The most direct evidence is our added training-objective intervention with a fixed AR scoring architecture (Table 2(e) in Section 6.3 / Appendix C). We compare standard NTP with catalog-normalized sequence-level training, Lcat-AR=−14log⁡qθ(c(i+)∣h)∑j∈Iqθ(c(j)∣h)\mathcal{L}_{\text{cat-AR}} = -\frac{1}{4}\log \frac{q_\theta(c(i^+)\vert h)}{\sum_{j \in \mathcal{I}} q_\theta(c(j)\vert h)}, retaining the same full-vocabulary AR architecture, SIDs, training events, and paired initialization, with the same 1/4 loss scaling, independent equal-budget LR searches, and exact full-catalog validation/testing. Unlike an already normalized legal tree, this full-vocabulary scorer assigns probability outside I\mathcal{I}, making catalog normalization a nonconstant, parameter-dependent change to the objective that supervises branches across all valid catalog items:

Fixed AR Scorer (3 Seeds)Beauty R@10Beauty N@10Toys R@10Toys N@10
Standard NTP0.05910.03150.05390.0281
Catalog-Normalized AR0.0662 (+12.0%)0.0364 (+15.6%)0.0665 (+23.4%)0.0367 (+30.6%)

We also clarify the scope of the explanation (Section 4.2 & Appendix C). The analysis concerns direct supervision of branch logits vs. complete-item scores for the current example. A single-step diagnostic on Table 2(d) shows that shared-parameter updates can change relative probabilities within non-target subtrees (0.0645 / 0.0669 mean absolute paired contrast on Beauty/Toys vs. a zero-gradient control), despite zero direct logit gradients there. The intervention shows that catalog-level competition improves ranking (+15.6% / +30.6% NDCG@10) with the AR scoring architecture retained. NRP also remains stronger in the independently tuned composed-history comparison.

Q3. Separate tuning, loss reduction, and history centering. The original Table 2(d) used a shared learning rate as a configuration control. We added independent, equal-budget searches over {5e-5, 1e-4, 3e-4, 1e-3, 3e-3} for LegalCE, StandardCE, and NRP on Beauty and Toys, with identical events, AdamW settings, and budgets (20-400 epochs; patience 10). Learning rates and checkpoints are selected solely by exact catalog validation, prioritizing NDCG@10, Recall@10, then earlier epochs (Appendix C):

Model (5-LR Grid, Exact Val/Test)Beauty N@10Toys N@10
Matched AR (StandardCE / LegalCE)0.03696 / 0.035720.03058 / 0.03087
NRP (Item CE)0.053680.05659

NRP leads on all metrics in both datasets. LegalCE averages over four SID tokens and valid events (event-mean item NLL/4), while NRP averages item NLL over events; under AdamW and our 5-LR grid, this 1/4 factor is absorbed. History centering is identical across all models (same centered D6 composer and bias-free query projection), and candidate centering adds only a common offset −qh⊤μ-q_h^\top \mu per query.

The DiGR comparison and the separate learning-rate sweeps answer my questions about the baselines. The result that moved my score was the improvement from catalog normalization with the AR architecture held fixed. That gives the supervision argument more support. I’ll raise my score to 3.

Thank you very much for taking the time to read our response and for raising your score. We are glad that the fixed-architecture catalog-normalization intervention, the separate learning-rate sweeps, and the matched DiGR comparisons addressed your questions. We will make sure all of these new results and clarifications are fully integrated into the revised manuscript.

Reviewer_K6b8OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper re-examines the coupling between semantic-ID representation sharing and autoregressive prediction in recommendation. It establishes that a legal SID tree with unrestricted node conditionals can represent any strictly positive catalog distribution, decomposes standard next-token loss into legal-tree and support terms, and contrasts target-path branch-logit supervision with catalog-wide item-score supervision. Motivated by this analysis, NRP uses a shared residual MLP to compose SID embeddings for both history encoding and candidate scoring, without an independent item embedding table. Experiments report competitive performance on three Amazon categories, substantial improvements over controlled autoregressive predictors, transductive cold-start benefits, and an additional evaluation on a 64K-item catalog.

Critical strengths

Separating the benefits of SID representation sharing from the choice of prediction interface is relevant to generative recommendation. The paper explicitly distinguishes unrestricted distributional expressivity from practical neural parameterization. The representation controls, cold-start protocol, and 64K-item inference measurements also help characterize where the proposed implementation is useful.

Critical weaknesses

The incremental contribution over existing SID-based item scoring is not sufficiently established. DiGR already explicitly separates the representational role of SIDs from token prediction and optimizes item-level likelihood using composed SID embeddings. VQ-Rec also precedes this work in constructing item representations from shared discrete-code embeddings for item-level recommendation. While the authors acknowledge these relationships in Appendix B.4, the proposed NRP prediction formulation itself remains close to this existing model family.

There is no end-to-end DiGR comparison. Table 19’s Mean variant is an internal aggregation control, which the paper explicitly distinguishes from reproducing DiGR; it uses the same fixed learning rate as the residual composer and omits catalog centering. The backbone-adapted VQ-Rec comparison also retains different tokenization and optimization settings. Consequently, the current evidence does not establish whether NRP improves on the closest existing approach, in particular how much of its improvement is attributable to composition, history encoding, and optimization choices rather than a new prediction principle.

The supervision analysis characterizes different output coordinates but does not establish the mechanism behind the accuracy gap. Equations (7)–(10) correctly distinguish derivatives with respect to local branch logits from derivatives with respect to complete-item scores. However, having nonzero derivatives for more item-score coordinates does not by itself imply more effective learning. The experiments primarily demonstrate a performance difference between practical parameterizations rather than test whether the proposed supervision distinction explains it. Changes in relative probabilities among two negative items are also not inherently beneficial, since the current target does not specify their relative relevance. Measurements of actual within-subtree probability changes, or a targeted intervention that varies catalog-level competition while retaining the same sequence scorer, would help connect the analysis to the practical learning behavior. Without such evidence, the analytical contribution remains a useful description of the models rather than a sufficiently established explanation of their ranking gap.

The comparisons leave important optimization and evaluation differences unresolved. The closest comparison in Table 2(d) uses the same learning rate and epoch limits, but the two formulations have different loss decompositions and gradient geometry. A shared training configuration is useful as a control, yet does not establish that both formulations receive adequate optimization. Appendix C.3 searches learning rates for the original AR-SID capacity variants, rather than the closest composed-history autoregressive model. In Appendix C.2, standard-CE checkpoints are selected using Beam20 validation before exact evaluation, introducing another avoidable difference from exact-ranking selection.

The broader comparisons also require qualification. Table 1 mixes locally evaluated results with published EAGER, COBRA, and DiffGRM numbers, for which matching categories and leave-one-out splitting do not guarantee identical preprocessing, candidate filtering, or inference settings. This matters especially for the small differences on Sports. In the cold-start study, item-level training excludes cold items from its denominator, while autoregressive training retains full token-vocabulary competition; the resulting difference in support supervision may contribute to the cold-target gap. A content-aware direct-scoring baseline and a warm-support autoregressive control would make that result more informative.

Questions for authors

See critical weaknesses. Here are some additional questions:

  1. What is the principal new conclusion relative to DiGR’s explicit separation of SID representation and item-level prediction? Can the authors provide a direct comparison under a common backbone, SID assignment, evaluation protocol, and comparable tuning budget? The internal Mean aggregation control does not resolve this comparison.

  2. Does the Table 2(d) gap persist after independent, equal-budget learning-rate searches for both formulations and exact-ranking validation for checkpoint selection? Please also specify loss reduction across SID positions and next-item events, and whether centering and output projections are aligned in this comparison.

  3. Do actual parameter updates preserve or substantially change relative probabilities within non-target subtrees, and does that behavior predict ranking errors? Alternatively, can the authors compare standard NTP with catalog-normalized sequence-level training using the same full-vocabulary autoregressive scorer? For an already normalized legal tree, path CE and complete-item NLL are identical, so simply rewriting that loss would not constitute a distinct intervention.

  4. How much of the cold-start advantage remains when autoregressive training normalizes over warm-catalog-valid continuations, and when NRP is compared with a content-aware item-scoring method such as VQ-Rec or DiGR? These controls would help separate compositional generalization from differences in candidate-support supervision.

2 comments
AuthorsOpenReview ↗

Response to Reviewer K6b8

Thank you for the constructive review. Below are our new results and planned revisions.

Q1. Contribution and comparison with DiGR. Building on DiGR's separation of SID representation and item prediction, we provide systematic theoretical analysis and progressively controlled evidence for retaining SID sharing while optimizing complete-item scores: (1) Legal SID trees have full catalog expressivity, yet matched controls (Table 2) show direct item scoring remains stronger under legal-branch normalization, aligned history/model designs, and exact catalog ranking; thus, invalid continuations or approximate search alone cannot explain the gap. (2) Under item cross-entropy, parameter-free pooling (DiGR/VQ-Rec) creates a bottleneck that NRP's residual MLP overcomes.

We ran 5-seed reproductions of original and GPT-2-adapted DiGR and VQ-Rec, plus EAGER, COBRA, and DiffGRM under our common protocol (updating Table 1 to 5-seed reproduced means, with published values in Table 6, Appendix B.3). DiGR (GPT-2) shares NRP's backbone, fixed RQ-KMeans SIDs, exact testing, and history filtering; NRP uses its fixed setting while DiGR (GPT-2) searches 33 LRs ×2\times 2 temperatures. NRP leads all metrics on all three datasets (e.g., Beauty Recall@10: 0.0928 for NRP vs. 0.0635 for DiGR, 0.0496 for DiGR (GPT-2), and 0.0798 for VQ-Rec (GPT-2)). Tuning all five composers (Table 22, Appendix D.4) over a 3×33 \times 3 LR/temperature grid without centering, Residual MLP (D=6D=6) achieves Beauty/Toys Recall@10 of 0.0944 / 0.0970 vs. 0.0508 / 0.0509 for the best simple aggregator (Sum), supporting our composition design.

Q2. Independent tuning and alignment for Table 2(d). The gap persists. We independently tuned LegalCE, StandardCE, and NRP over {5e-5, 1e-4, 3e-4, 1e-3, 3e-3} with identical events, AdamW settings, and budgets (20-400 epochs; patience 10), selecting by exact catalog validation (prioritizing NDCG@10, Recall@10, then earlier epochs; Section 6.3 / Appendix C):

Model (5-LR Grid, Exact Val/Test)Beauty N@10Toys N@10
Matched AR (StandardCE / LegalCE)0.03696 / 0.035720.03058 / 0.03087
NRP (Item CE)0.053680.05659

LegalCE averages over 44 SID positions and events (item NLL/4\text{NLL}/4), while NRP averages item NLL over events; under AdamW and our 5-LR grid, this 1/41/4 factor is absorbed. All three share the D=6D=6 composer, identical history centering, and bias-free query projection. For fixed query qhq_h, candidate centering adds a common offset −qh⊤μ-q_h^\top \mu, leaving softmax and rankings unchanged.

Q3. Subtree updates and fixed-scorer intervention. A single-step diagnostic on Table 2(d)'s legal predictor shows shared-parameter updates alter relative probabilities inside non-target subtrees (0.0645 / 0.0669 mean absolute paired difference in log-odds change on Beauty/Toys vs. a zero-gradient control, Appendix C), reflecting untargeted collateral drift rather than direct competitive suppression.

Following your suggestion, using the same full-vocabulary AR architecture, SIDs, events, and paired initialization, we compared standard NTP with catalog-normalized sequence training, Lcat-AR=−14log⁡qθ(c(i+)∣h)∑j∈Iqθ(c(j)∣h)\mathcal{L}_{\text{cat-AR}} = -\frac{1}{4}\log \frac{q_\theta(c(i^+)\vert h)}{\sum_{j \in \mathcal{I}} q_\theta(c(j)\vert h)} (the same 1/4 loss scaling, equal-budget LR searches, exact catalog validation/testing). While normalized legal-tree path CE equals item NLL, the full-vocabulary scorer assigns mass outside I\mathcal{I}, so normalizing over I\mathcal{I} adds a nonconstant, parameter-dependent term that propagates repulsive gradients to non-target catalog items (Table 2(e) / Appendix C):

Fixed AR Scorer (3 Seeds)Beauty R@10Beauty N@10Toys R@10Toys N@10
Standard NTP0.05910.03150.05390.0281
Catalog-Normalized AR0.0662 (+12.0%)0.0364 (+15.6%)0.0665 (+23.4%)0.0367 (+30.6%)

Thus, catalog-level competition improves ranking with the AR head fixed. NRP also remains stronger in the independently tuned composed-history comparison.

Q4. Cold-start controls (Warm AR and DiGR). On Beauty's 10% holdout (Table 4 / Appendix E): (1) Warm AR normalizes training over warm-catalog-valid continuations and tests via exact catalog scoring; cold Recall@10 rises from AR-SID's 0.0005 to 0.0104, confirming training-support effects, while NRP still exceeds Warm AR by +48.1% in cold Recall@10 (0.0154 vs. 0.0104) and +65.8% in NDCG@10. (2) Content-aware item-scoring DiGR leads on cold targets, while NRP ranks 2nd on cold and 1st on warm targets (+41.3% / +51.6% warm Recall@10 / NDCG@10 over DiGR), reflecting a specialization-smoothing trade-off: DiGR's parameter-free pooling underfits warm collaborative signals, whereas NRP's learned composer achieves top warm accuracy alongside strong cold-start generalization.

Dear Reviewer K6b8,

As the discussion period is drawing to a close in about two days, we wanted to kindly follow up to see if our response and new experiments have addressed your concerns.

In particular, we would like to thank you again for suggesting the fixed-scorer sequence-level catalog-normalization intervention in Q3. Conducting this exact experiment yielded a clear +15.6% and +30.6% NDCG@10 improvement on Beauty and Toys without changing the AR scoring architecture, providing the direct evidence needed to connect catalog-level competition to ranking gains. Together with our matched 5-seed DiGR/VQ-Rec comparisons and composer tuning (Q1), independent equal-budget learning-rate sweeps with exact validation for Table 2(d) (Q2), and the Warm-AR and DiGR cold-start controls (Q4), we hope these results fully resolve your questions.

Please let us know if there are any remaining points we can clarify before the discussion window closes. Thank you again for your time and constructive feedback!

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

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