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Paper summary
This paper revisits the effectiveness of joint training of Semantic ID (SID) tokenizers and generative recommenders, compared with the conventional two-stage training paradigm. Through controlled experiments across five Amazon recommendation datasets, the authors find that joint training does not consistently outperform a carefully tuned two-stage baseline and can even lead to performance degradation.
To explain this phenomenon, the paper proposes the update bottleneck hypothesis, which highlights the tension between discrete SID stability and tokenizer adaptability. Specifically, tokenizer updates may have limited effects on the recommender when discrete assignments remain unchanged, while frequent SID reassignments can disrupt recommender optimization. The authors provide a theoretical analysis of this issue and introduce diagnostic metrics, including exposure-weighted reassignment mass and embedding displacement. Additional experiments investigate gradient connectivity, codebook tying, and different tokenizer update configurations.
The findings provide empirical evidence that joint optimization does not necessarily improve generative recommendation and offer insights into the challenges of learning through discrete representation interfaces.
Critical strengths
The paper revisits an important assumption in Semantic ID-based generative recommendation: that jointly optimizing tokenizers and recommenders should naturally outperform a two-stage training approach. The reported negative results challenge this assumption and provide useful insights into the potential limitations of joint training. In particular, the distinction between gradient connectivity and actual changes in discrete representations offers an interesting perspective on understanding optimization behavior in SID-based recommendation systems.
The paper provides relatively rigorous empirical evaluations, including multiple random seeds, statistical significance analyses, and controlled experiments examining different sources of tokenizer updates. The proposed diagnostic metrics offer a useful way to characterize SID reassignment and representation instability during training. The analyses of codebook tying and delayed tokenizer updates further strengthen the empirical investigation and provide practical insights into the interaction between tokenizer updates and recommender learning.
Critical weaknesses
My primary concern is that the experimental evidence may not be sufficient to support the broader conclusions regarding the limitations of joint training. Although the authors conduct carefully controlled comparisons, the joint-training configurations are not independently optimized for each dataset. In particular, the use of hyperparameters initially tuned on Beauty may disadvantage joint training on other datasets, where the optimal tokenizer learning rate, update frequency, or optimization schedule could differ substantially. Moreover, freezing the tokenizer encoder in the main Beauty joint-training experiments limits the extent to which the framework explores the potential benefits of fully end-to-end optimization. Consequently, the observed performance degradation may partly reflect the specific training configurations rather than an inherent limitation of joint SID learning. Stronger per-dataset tuning and experiments with more flexible joint-training configurations are needed to substantiate the generality of the findings.
Although the update bottleneck hypothesis is intuitively reasonable, its empirical validation remains somewhat limited. The theoretical analysis mainly formalizes properties of discrete interfaces and provides qualitative bounds, but does not establish when the proposed bottleneck necessarily leads to worse recommendation performance. More importantly, the key diagnostic analyses of SID reassignment and embedding displacement are conducted on a limited number of datasets and random seeds. The observed relationship between representation instability and recommendation performance is suggestive, but does not fully establish that the proposed bottleneck is the primary cause of joint-training degradation. Alternative factors, including optimization instability, representation quality, and differences in content-embedding backbones, may also contribute to the results. More systematic experiments that directly manipulate SID stability while controlling other factors would strengthen the proposed explanation.
Questions for authors
Could the authors provide additional joint-training experiments with independently tuned hyperparameters for each dataset, particularly tokenizer learning rates, update schedules, and SID refresh frequencies? Do the observed performance degradations persist after such tuning?
What is the rationale for freezing the tokenizer encoder in the main joint-training experiments on Beauty? How does performance change when the encoder is jointly optimized with the recommender, potentially with appropriate regularization or stabilization techniques?
Could the authors provide more direct evidence that SID reassignment and embedding displacement are responsible for the observed performance degradation? For example, would explicitly controlling the reassignment rate through stability regularization or alternative update schedules improve recommendation performance under otherwise identical conditions?
Since the experiments use different content-embedding backbones across datasets, could the authors evaluate whether the observed differences between Beauty and the other datasets persist when using the same backbone? This would help disentangle dataset-specific effects from differences introduced by the representation models.
Have the authors considered retraining a recommender from scratch using the final SIDs obtained from joint training? Such an experiment could help distinguish whether joint training produces inferior final representations or whether its performance degradation mainly arises from changing SID assignments during recommender optimization.
Could the authors extend the key reassignment and embedding displacement analyses to additional datasets and random seeds? In particular, does the relationship between the proposed diagnostic metrics and downstream recommendation performance remain consistent across different settings?
3 comments
Why the encoder is frozen. Training the encoder lowers accuracy sharply on Beauty (by about a fifth to a third of NDCG@10), and the drop happens even with the recommendation gradient blocked: the tokenizer's own losses collapse the semantic IDs, so most items stop having a unique code. Stabilizers we tried recovered at most a quarter of the drop. The codebooks still train in every joint run, and DIGER's released scripts also freeze the encoder. We will add these results to the appendix.
"The observed relationship between representation instability and recommendation performance is suggestive, but does not fully establish that the proposed bottleneck is the primary cause of joint-training degradation."
We now measure the disruption directly: when item codes change, the recommender's validation loss jumps at that moment, with nothing else changed. We extended the diagnostics to all seeds and both datasets, directly controlled how often codes change, and tested a shared embedding backbone.
1. Direct evidence: validation loss jumps when codes change. We logged validation loss immediately before and immediately after every code recompute (tuned setting, 6 seeds each). Nothing else changes between the two measurements: the recommender's weights are the same; only the item codes differ.
| Toys, tied | Toys, untied | Beauty, tied | Beauty, untied | |
|---|---|---|---|---|
| Recomputes that raise validation loss | 93% | 93% | 62% | 85% |
| Mean validation-loss rise per recompute | 0.0026 | 0.0064 | 0.0007 | 0.0023 |
| Items whose final code differs from their initial code | 10.1% | 18.3% | 2.7% | 7.1% |
- Training-batch loss rises by a similar amount at each recompute (Toys tied 0.0029, untied 0.0072), so the rise is not noise in the validation set.
- The rise is larger where more codes change: on Toys more than on Beauty, and in untied more than in tied training.
- The untied runs answer the concern about the tied codebook pathway. Untied training has no continuous pathway from the codebook to the recommender: the recommender reads its own embedding tables. Its jumps can therefore come only from code changes, and they are the largest we observe. This reinforces the paper's claim that changing item codes disrupts the recommender's learning.
- The recommender then has to recover: in 71–85% of epochs, validation loss falls back below its post-recompute level by the next epoch.
These measurements are the immediate loss change that Equation 5 bounds. Equation 5 does not give the sign of this change, but the measurements show that the loss rises at most recomputes.
2. Repeated changes and reversals. Table 4 compared only each item's first and last code, so it could miss items whose code flips back and forth. We now saved every item's code at every epoch, for all 6 seeds on both datasets. In tied training, 4.8% of Toys items and 0.7% of Beauty items change code two or more times, and 4.1% and 0.7% go back to a code they had before. Most changes happen early in training (Toys: 0.35% of items change code per epoch in epochs 0–9, 0.09% after epoch 75). So code changes are not a one-time switch: some items keep flipping, mostly early, and about seven times more often on Toys than on Beauty. This matches the association in the paper: the dataset with more repeated code changes (Toys) is the one where joint training does worse.
3. Displacement on both datasets, all seeds. We saved every epoch's codebook for all 6 seeds on Toys and Beauty. At the reported checkpoint, codebook vectors have moved, as a share of their initial length (levels 1 / 2 / 3): tied training 3.0% / 9.5% / 17.8% on Toys and 0.8% / 1.7% / 1.8% on Beauty; untied training 6.8% / 10.7% / 13.5% on Toys and 2.1% / 3.7% / 4.3% on Beauty. Displacement is several times larger on Toys, where joint training does worse, matching the paper's Beauty-only observation.
4. Are the final codes inferior, or is adapting to changing codes the problem? We trained a fresh two-stage recommender on each joint run's final codes (Beauty, 6 seeds, paired by seed, paper settings):
| Recommender | Recall@10 | NDCG@10 | NDCG@10 minus two-stage on original codes |
|---|---|---|---|
| Two-stage, original codes | 0.0704 | 0.0388 | — |
| Two-stage, final joint-training codes | 0.0708 | 0.0389 | +0.0001 (p = 0.83) |
On Beauty, the final codes are neither better nor worse than the original codes. So joint training does not result in IDs that are more favorable towards a separate recommender training either.
5. Controlling SID stability. Recomputing codes less often, or never, gives the same final accuracy. The recommender recovers from each setback, but changing codes never bring a lasting gain.
6. Same backbone. With the same Qwen embeddings as the other datasets, Beauty also loses with joint training. The embedding backbone decides whether tying helps; in no case does the recommendation gradient produce the gain.
We now tune every method separately on each dataset. After tuning, the recommendation gradient into the tokenizer still adds nothing over a tuned two-stage pipeline. We keep the encoder frozen because training it collapses the semantic IDs.
We added untied joint training: the recommender keeps its own embedding tables, while the recommendation gradient still reaches the tokenizer's codebook. We ran it with the recommendation gradient on and off. (With the gradient off, only the recommendation loss is blocked from reaching the tokenizer. The tokenizer still trains on its own losses during recommender training and item codes are still recomputed every epoch.) We used Toys, where joint training had lost in the original setup, and Beauty, where it gained in the original setup.
For these runs, two-stage, tied joint and untied joint training each got their own hyperparameter search (grid in reviewer QQds's last comment). Note that this was also one of the common issues raised by the reviewers, which is that we did not perform hyperparameter search for each individual arms. We do this for values presented in the rebuttal. Each gradient-off arm uses the same setting as its gradient-on counterpart, so we can isolate the effect of recommender gradient reaching the tokenizer alone. For each arm, we run 6 seeds at its best hyperparameter setting. We compute mean differences paired by seed, with 95% paired-t confidence interval.
Toys (differences: arm minus two-stage, paired by seed, [95% CI]; bold: joint training is not significantly better than two-stage, i.e. the interval includes 0 or lies below 0)
Beauty (same format)