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Information Retrieval · arXiv:2610.39352 v1 · submitted 29 Oct 2026 · 45 references

Try Before You Evolve: Ranking-Scored Trials for Recursive Self-Improvement of Recommender Systems

Xu Huang, Jiawei Feng, Jiancan Wu

The paper says

“Recommenders on Web platforms such as e-commerce and music streaming need their training recipes re-tuned for each dataset. Large language model (LLM) agents can now rewrite these recipes, enabling recursive self-improvement (RSI) of recommender systems.”

more of the abstract

Existing agents propose one edit per round, fully retrain the recommender, and keep the edit only if its ranking quality improves. Unlike programs or patches that can be scored by execution, a recommender edit changes how the model is trained, which raises two challenges. First, ranking feedback is delayed: an edit's ranking quality is known only after full retraining, so much of the retraining budget goes to edits that are later discarded. Second, the signals available before retraining are unreliable: sampled training losses can look solved while full-ranking performance remains poor, and they are not comparable across edits that change the loss or sampler. We propose RecRSI, which generates diverse candidate edits from a diagnosis of the current model and selects one for full retraining using early ranking feedback: each candidate receives a short trial, the first steps of its full training run, scored by full-ranking NDCG@10 on held-out probe users. With two sequential recommenders on three datasets and the same number of full retrainings, RecRSI significantly outperforms existing self-evolving agents in every setting, and on both Amazon datasets reaches in its first round a ranking quality that none of them reaches in five.

from the abstract

Pith says

Machine review · deepseek-v4-flash · 30 Oct 2026 · what was read was not recorded · not checked by a person

It can be wrong. Challenge this review or reply to it.

Holds up, with conditions. A solid, unusually careful empirical paper: trial-based selection among LLM-proposed edits clearly beats the alternatives, but the 'outperforms existing agents' headline rests on re-implementations that were never calibrated against the originals. This line is wrong

2 major objections · 6 minor

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Not checked: figures, code, what the 45 references say.

The paper says, at Abstract [b7]; Appendix C; Section 2.2

The review did not quote this passage.

Pith says: Objection 1 of 2 · major

The abstract's central claim that RecRSI 'significantly outperforms existing self-evolving agents in every setting' is established only against the shared-harness re-implementations of AlphaEvolve, DeepEvolve, and Self-EvolveRec described in Appendix C, and no calibration against the published agents is reported: no original code is run and no output comparison is given.

more of objection 1

The manuscript's own text carries adaptation-stress signals: four Self-EvolveRec retrainings fail before training starts (Section 2.2), its first SASRec edit is kept only in round 3 on CDs and round 4 on Office (Section 2.2), and its HSTU Office final NDCG@10 of 0.0082 barely exceeds the initial 0.0070 (Table 2). These patterns are consistent with prompt-heavy machinery (simulated user critiques, retrieval-reflection, archive sampling) degrading under the shared GLM-5.3 prompter, and since the largest claimed margins (HSTU Office +102.0%, SASRec Office +41.5%) are computed against the weakest baseline rows, even a moderate fidelity gap would materially shrink the headline gains. The shared-harness design is defensible for isolating the selection mechanism, and Appendix C is transparent about re-implementation; what is unresolved is the wording of the headline. I ask for a calibration check on at least the Self-EvolveRec CDs setting (whose split and version the paper adopts), or a scoped statement in the abstract and Section 4.2 that the comparison is against shared-harness re-implementations; the internal comparisons (the K=1 variant and First-of-3 in Section 4.3 and Table 3) do not depend on baseline fidelity and already support the mechanism claim.

The paper says, at Section 4.1.3, Section 4.2, Table 2

The review did not quote this passage.

Pith says: Objection 2 of 2 · major

The statement that 'all 36 paired comparisons with a baseline are significant' comes from paired bootstrap over Test users for the single retained trajectory in each setting, and the abstract's 'significantly outperforms' inherits that scope. Because the LLM samples at temperature 0.5 and training is stochastic, every cell of Table 2 is one draw from a distribution over evolution trajectories; the bootstrap covers Test-user sampling but not trajectory variance, so the significance statement is narrower than its wording.

more of objection 2

The margins are large and consistent across all six settings, so I do not doubt the direction of the effect, but I ask that the authors either run a few independent trajectories for at least the key comparisons (e.g., SASRec and HSTU on CDs, or the Section 4.3 selection signals), or reword the abstract and Section 4.2 so that 'significant' is stated as within-trajectory significance over Test users on the reported runs.

6 minor objections

The paper says, at Section 4.2, Table 2

Pith says: minor objection 1 of 6

The 36 pairwise comparisons are reported without intervals or any multiple-comparison correction; since the equal-budget comparison already reports bootstrap intervals with a Bonferroni correction (Appendix G, Table 7), the same presentation for the main table would make the claim easier to verify.

The paper says, at Section 3.2, Appendix A

Pith says: minor objection 2 of 6

Add a sensitivity sweep for the trial length K_s and the promotion margin delta in at least one setting (e.g., SASRec on CDs); the trial length is acknowledged as unexplored in Appendix A, and a sweep would bound how sensitive the kept rates and margins are to these two free parameters.

show 4 more

The paper says, at Appendix G

Pith says: minor objection 3 of 6

The equal-GPU budget intentionally does not equalize LLM token usage, as the appendix states; because RecRSI sends longer prompts (diagnosis, memory, and K edits per round), reporting per-method token counts would complete the cost comparison.

The paper says, at Section 4.3, Table 4 and Figure 3

Pith says: minor objection 4 of 6

The aggregate comparison of selection signals mixes the signal's effect with the effect of divergent parents after round 1 (the paper notes that candidate sets differ after the first round); a round-1-only breakdown of Table 4, where the parent is shared, would make the causal attribution of the 'strongest and safest' claim airtight.

The paper says, at Section 4.1.5

Pith says: minor objection 5 of 6

Specify how the fixed subset of 12,000 probe users for Office trials is chosen (e.g., the first 12,000 users under the fixed hash), since the probe set contains 89,528 users and the subset definition matters for reproducibility.

The paper says, at Full manuscript

Pith says: minor objection 6 of 6

The typeset text contains stray markup tokens such as '</>' and a 'Conference'17, Washington, DC, USA, 2027' placeholder in the header; these should be cleaned before resubmission.

What would settle it

Run the original released code of Self-EvolveRec — the strongest baseline in most settings and the one with the most bespoke machinery — under the shared five-round protocol on the released CD split that Appendix B reuses unchanged (using GLM-5.3, or documenting the model mapping), and compare per-round select NDCG@10 and final Test NDCG@10 against the Appendix C re-implementation; then repeat for AlphaEvolve and DeepEvolve on at least one setting. If an original implementation reaches more than 10% higher relative NDCG@10 on any setting, the re-implementations suffer adaptation loss and the headline margins must be recomputed; if both match within noise, the comparative claim stands.

from the skeptic's reading

How the review went

4 readings by deepseek-v4-flash · 30 Oct 2026

  1. Reader holds up, with conditions confidence high
  2. Skeptic agrees 1 min 31 s · 23,482 tokens read, 16,748 written
  3. Editor wrote the verdict above 32 s · 24,567 tokens read, 5,497 written
  4. Referee major revision: 2 major objections, 6 minor 2 min 2 s · 23,826 tokens read, 21,849 written

Not run on this paper: the simulated authors' defence.

Pith did not check this review's objections against the paper.

The review in full

The review in brief, machine-written

Two things to know. This is a careful empirical paper about a simple idea that works: instead of retraining an LLM agent's first proposed edit, propose three edits, run each for 15% of the training budget, score by full-ranking NDCG@10 on probe users, and fully retrain the one that scores best. And: the internal evidence for that mechanism is strong, but the headline against "existing self-evolving agents" rests on re-implementations that were never calibrated against the originals. That is the one thing that could genuinely shrink the reported margins.

What is new: the short-trial mechanism is explicitly borrowed from multi-fidelity HPO, and the paper says so. The adaptation is the point — open-ended LLM edits that rewrite the loss or sampler break the shared-objective assumption of Hyperband-style search. The design principles, training consistency and ranking consistency (the trial measures exactly what the outcome reward measures, just earlier), are stated sharply and operationalized cleanly.

What is done well: the equal-GPU-hour comparison charges trial costs; the ablations hold the proposer fixed and swap only the selection signal; prospective (Section 4.3) and retrospective (Appendix D) evidence are separated and labeled; probe/select/Test isolation is clean, with Test touched once. Crucially, the trial-outcome correspondence is measured, not assumed: rho = 0.46, AUC 0.71, honestly moderate. The safety result is real — worst select drop 5.3% for trials versus 20–83% for the alternatives. Trial length, five-round horizon, and single LLM are all acknowledged limitations.

Soft spots, in proportion. Baseline fidelity is the real one. AlphaEvolve, DeepEvolve, and Self-EvolveRec are re-implemented in a shared GLM-5.3 harness (Appendix C); no original code is run, and no output comparison is reported. The text carries adaptation-stress signals: four Self-EvolveRec retrainings fail before training starts [b59], its first kept SASRec edit comes only in round 3 on CDs and round 4 on Office, and its HSTU Office final (0.0082) barely exceeds the initial model (0.0070). The biggest margins (HSTU Office +102%, SASRec Office +41.5%) are against the weakest rows. The authors are transparent that they re-implemented, and an equal-LLM shared-harness comparison is defensible; what is missing is a calibration check. Note the core contribution survives this concern: the ablation results hold the proposer fixed, so trial selection beating random, LLM-judge, and warm-start selection does not depend on baseline fidelity.

Single trajectory per setting: significance is over Test users within one run, so LLM proposal stochasticity (temperature 0.5) sits outside the error bars. One or two repeated trajectories per setting would have been cheap relative to the study. Minor: the trial length (15%) is fixed with no sensitivity study, and the abstract's claim that both Amazon datasets reach five-round quality in the first round is slightly stronger for CDs, where the shown feat is beating the others' one-hour results.

Who this is for: people building LLM agents for recommender development, and anyone doing self-improving training-code search with an expensive evaluator. It deserves a serious referee. The revision demands are standard and satisfiable: code and per-round artifacts, a calibration or honest rescoping of the baseline comparison, and a few repeated trajectories. Send it to review.

The strongest objection

The abstract's central claim [b7] — RecRSI 'significantly outperforms existing self-evolving agents in every setting' — requires that the Appendix C re-implementations of AlphaEvolve, DeepEvolve, and Self-EvolveRec preserve the behavior of the published systems once adapted to the shared GLM-5.3 harness. That condition is never checked: no original code is run and no output comparison is reported. The paper's own text carries adaptation-stress signals: four Self-EvolveRec retrainings fail before training starts [b59]; Self-EvolveRec keeps its first SASRec edit only in round 3 on CDs and round 4 on Office (Section 2.2); and its HSTU Office final NDCG@10 of 0.0082 barely exceeds the initial 0.0070 (Table 2). These are exactly the patterns expected if prompt-heavy machinery — Self-EvolveRec's simulated user critiques and diagnosis co-evolution, DeepEvolve's retrieval–reflection loop, AlphaEvolve's archive sampling — degrades when re-implemented on GLM-5.3 without the original prompt engineering. The largest margins (HSTU Office +102.0%, SASRec Office +41.5%) are computed against the weakest baseline rows, so a fidelity gap of even 10–20% relative on those rows would materially shrink the claimed gains, and the abstract's 'outperforms existing agents' wording would be unsupported. This is not an internal inconsistency, and the equal-LLM, shared-harness design is methodologically defensible; the paper is transparent that it re-implements (Appendix C). The unresolved point is that the comparative headline is asserted about the published agents while the evidence concerns the authors' adaptations, with no calibration check. The single-trajectory-per-setting design and the fixed 15% trial length are additional verification gaps, but they do not bear on the comparative headline as directly: the fidelity question is the one whose failure would falsify the abstract.

I agree with the reader: baseline fidelity is the most load-bearing condition for the central claim. The mechanism claim — that trial-scored selection beats random, LLM-judged, and warm-start selection by the same proposer — is internally well supported (Section 4.3), and the equal-GPU comparison (Table 3, Appendix G) shows the win survives when trial costs are charged, with Test kept out of the search (Appendix B). The retrospective correlation analysis is properly labeled as retrospective [b292], and the prospective ablations carry the load. What remains unverified is the external anchor of the headline: the three baselines are re-implementations on the authors' harness with a single LLM (GLM-5.3), and nothing calibrates these adaptations against the published systems. The risk signals are concrete and appear in the paper's own text: four Self-EvolveRec retrainings fail before training starts [b59]; its first SASRec edit is kept only in round 3 on CDs and round 4 on Office (Section 2.2); and its HSTU Office result (0.0082) barely exceeds the initial model (0.0070) in Table 2. If these reflect adaptation loss rather than genuine difficulty, the 102.0% HSTU Office and 41.5% SASRec Office margins are inflated precisely where the baseline rows look weakest. I also checked the Table 2 arithmetic as a possible independent concern: with four-decimal rounding the stated NDCG improvement percentages reproduce within about one percentage point (e.g., HSTU Office 0.0199/0.0099 computes to +101.0% versus the stated +102.0%), so rounding explains the discrepancy and this is not a further issue. The single-trajectory-per-setting design is a genuine secondary gap, but the consistency of RecRSI leading in all six settings and under the equal-GPU budget mitigates it, and additional seeds would tighten rather than refute the mechanism claim. Baseline fidelity is the one failure mode that would directly falsify the abstract's comparative sentence, and it is the one the authors can settle: they already reuse Self-EvolveRec's released CD split, so a calibration run against the original implementation is well-defined. I therefore keep the reader's CONDITIONAL verdict unchanged, with the existing conditions (working code release, per-round artifacts, fidelity check, and ideally multi-seed confirmation) as the path to acceptance.

The referee's report

If the results hold, the contribution is a simple, well-motivated selection principle for recommender RSI: score an edit by a low-fidelity run of the exact training procedure and the exact full-ranking metric, rather than by loss curves or an LLM's judgment of the patch. The methodology is unusually careful: the ablations in Section 4.3 hold the proposer and batch size fixed and vary only the selection signal; the equal-GPU-hour protocol charges trial costs and is described precisely (Appendix G); probe, select, and Test users are isolated with per-level details (Appendix B); prospective (Section 4.3) and retrospective (Appendix D) evidence are separated honestly; and the negative result for the LLM judge is reported rather than buried. The trial score is by construction a prefix of the evaluated run, but the paper treats the trial-outcome correspondence as an empirical quantity (rho=0.46, AUC 0.71, Table 6) instead of assuming it, so the design is not circular in a damaging way. The per-round traces (Appendix E) and the parent-trial reference rule (11 of 13 promotions when the selected edit beats the parent trial versus 2 of 7 otherwise, Section 4.4) are concrete and checkable.

Pith's reading of the paper (a machine's summary, not the authors')

This paper tries to fix a wastefulness in LLM-driven recommender development: when an LLM agent rewrites a recommender's training code, the only trustworthy way to judge a rewrite used to be to fully retrain the model and measure ranking quality, so most retraining runs were spent on edits that were later discarded. The authors claim that a short trial run — the first steps of the edit's own training trajectory from the same initialization, scored by full-ranking NDCG@10 on held-out probe users — reliably predicts which edit deserves the full retraining, with no learned reward model. With this trial-first selection, they report that RecRSI outperforms three existing self-evolving agents in all six settings tested (two backbones, three datasets) at the same number of full retrainings, with Test NDCG@10 gains of 16.1% to 102.0%, and keeps 23 of 30 retrainings versus 37 of 90 for the baselines. If right, this makes recursive self-improvement of recommenders both cheaper and safer, because the signal used to pick an edit is the same full-ranking measurement later used to accept it.

What carries the argument. The short trial is the load-bearing object: a training run of an edited recipe from the shared initialization $\theta^{(0)}$ with seed $\xi$, executed for the first $K_s$ steps of the recipe's own full-training schedule (here $K_s = 4{,}000$, about 15% of the 26,000-step budget, with no early stopping), then scored by full-ranking NDCG@10 on held-out probe users. It carries the argument through two properties: training consistency, which ensures the trial observes the same training process the full retraining would observe, so edits that add parameters need no weight transfer from the parent and loss- or sampler-changing edits are evaluated under their own objectives; and ranking consistency, which ensures all candidates are compared on the metric that later decides promotion, so losses on different scales do not corrupt the choice, and computing the score on probe users keeps the select users that rule on promotion out of the selection. The parent recipe run through the same trial supplies a reference score $m_p$, which the paper shows predicts promotion: when the selected candidate beats $m_p$, 11 of 13 retrainings are promoted, versus 2 of 7 when it does not.

Core claim. The paper's central claim is that candidate recommender-code edits can be compared before committing a full retraining, by running each edit for the first $K_s$ steps of its own training schedule from the shared initialization $\theta^{(0)}$ and scoring the resulting model by full-ranking NDCG@10 on held-out probe users — a signal it calls the short trial. The paper argues this signal has the two properties that make the outcome reward trustworthy: training consistency, because the trial follows exactly the edited training procedure a full retraining would follow, so edits acting through the loss, sampler, optimizer or architecture are evaluated on their own terms; and ranking consistency, because the trial uses the same full-ranking evaluator, item set and tie handling as the promotion metric, so edits trained with different objectives remain comparable. On this basis the paper reports that RecRSI — three diverse, diagnosis-conditioned edits per round, each tried for about 15% of the step budget, the best-scoring one retrained and kept if it improves select-user ranking — outperforms AlphaEvolve, DeepEvolve and Self-EvolveRec in all six backbone-dataset settings by 16.1% to 102.0% in Test NDCG@10, promotes 23 of 30 retrainings against 37 of 90 for the baselines, and reaches in its first round a ranking quality that no baseline reaches in five on both Amazon datasets. The ablations attribute the gain to the trial itself: random choice, an LLM judge, and warm-start continuations all end lower on average, and executed signals correlate positively with retraining outcomes ($\rho = 0.46$, AUC 0.71 for the short trial) while the non-executed LLM judge correlates negatively ($\rho = -0.14$).

The premise it rests on. The comparative headline assumes that the paper's re-implementations of AlphaEvolve, DeepEvolve and Self-EvolveRec in the shared harness faithfully reproduce the published systems' behavior, because the original code was not run, no output comparison against it is reported, and the shared GLM-5.3 prompter could systematically disadvantage a baseline designed around different prompting.

If the paper is right (Pith's inferences, not the authors')

With the same number of full retrainings, an evolution loop that tries several edits briefly and retrains the best-scoring one reaches higher ranking quality than any of the three single-edit proposers, with reported Test NDCG@10 gains of 16.1% to 102.0% across all six backbone-dataset settings.

Because the trial reuses the full-retraining code and the full-ranking evaluator and needs no learned reward model, the selection step can be inserted into existing recommender agents that currently retrain their first proposal, at the cost of the trial runs.

Short trials act as a safety filter: RecRSI never retrained an edit that lost more than 5.3% of its parent's select NDCG@10, whereas every alternative selection signal retrained at least one edit losing more than 20%.

The parent's own trial score is an early-stopping signal: when the best candidate beat the parent trial, 11 of 13 retrainings were promoted, versus only 2 of 7 when it did not, so rounds with $m_{a^\star} \le m_p$ could skip the retraining entirely.

The advantage survives when the trials are charged against a fixed GPU budget: at one GPU hour on SASRec/CDs, RecRSI completes fewer rounds than the alternatives yet ends with the highest NDCG@10, so full retrainings themselves, not raw compute, are the resource the method spends well.

The trial protocol generalizes beyond recommenders: any setting where judging a code edit requires an expensive training run and sampled or proxy signals hide true performance — fine-tuning pipelines, distillation, or LLM post-training — could rank candidate recipes by a short run scored with the final metric.

The paper fixes the trial length at about 15% of the step budget, the batch size at three edits, and the repair policy at one attempt; a natural extension would adapt the trial budget per round, for instance lengthening trials when the top candidate and the parent's trial score are close.

Because trials only filter proposals, the ceiling of the method is set by the proposer's diversity; a testable consequence is that RecRSI's margin over single-edit agents should shrink as the LLM's proposal diversity is degraded, for example by removing the component-diversity instruction from the prompt.

The paper's split of validation users into probe (choice) and select (promotion) sets invites scrutiny of the probe set itself: if repeated probing of the same probe users over many rounds distorts later selections, the margin should decay across rounds, which the per-round records in Appendix E would reveal.

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The paper

Abstract

Recommenders on Web platforms such as e-commerce and music streaming need their training recipes re-tuned for each dataset. Large language model (LLM) agents can now rewrite these recipes, enabling recursive self-improvement (RSI) of recommender systems. Existing agents propose one edit per round, fully retrain the recommender, and keep the edit only if its ranking quality improves. Unlike programs or patches that can be scored by execution, a recommender edit changes how the model is trained, which raises two challenges. First, ranking feedback is delayed: an edit's ranking quality is known only after full retraining, so much of the retraining budget goes to edits that are later discarded. Second, the signals available before retraining are unreliable: sampled training losses can look solved while full-ranking performance remains poor, and they are not comparable across edits that change the loss or sampler. We propose RecRSI, which generates diverse candidate edits from a diagnosis of the current model and selects one for full retraining using early ranking feedback: each candidate receives a short trial, the first steps of its full training run, scored by full-ranking NDCG@10 on held-out probe users. With two sequential recommenders on three datasets and the same number of full retrainings, RecRSI significantly outperforms existing self-evolving agents in every setting, and on both Amazon datasets reaches in its first round a ranking quality that none of them reaches in five.

The paper's own sentences, arranged, kept beside the review and separate from it. Each label is drawn from a closed vocabulary; the number beside it is the probability the classifier gave that label. No sentence in this record was written by a model.

abstract compiled · 2026-10-30

The authors' main claim, as the classifier picked it out 1.00

“With two sequential recommenders on three datasets and the same number of full retrainings, RecRSI significantly outperforms existing self-evolving agents in every setting, and on both Amazon datasets reaches in its first round a ranking quality that none of them reaches in five.”

How the main claim is stated: asserted 1.00

What the abstract itself states, as probabilities: claims first 0.09 · states limitation 0.14 · human participants 0.05 · controlled comparison 0.91 · randomized assignment 0.02 · states quantitative result 0.78 · compares with prior results 0.98 · mentions code or data availability 0.03

The abstract, sentence by sentence

This table labels the abstract only (arXiv listing abstract v1). The number is the probability the classifier gave the label.

SentenceRoleThe authors' own workStates the main conclusionStrength
Recommenders on Web platforms such as e-commerce and music streaming need their training recipes re-tuned for each dataset. background 1.00 0.07 0.01 asserted 1.00
Large language model (LLM) agents can now rewrite these recipes, enabling recursive self-improvement (RSI) of recommender systems. background 1.00 0.07 0.02 asserted 0.88
Existing agents propose one edit per round, fully retrain the recommender, and keep the edit only if its ranking quality improves. background 0.96 0.05 0.03 asserted 1.00
Unlike programs or patches that can be scored by execution, a recommender edit changes how the model is trained, which raises two challenges. gap 0.59 0.11 0.02 asserted 0.99
First, ranking feedback is delayed: an edit's ranking quality is known only after full retraining, so much of the retraining budget goes to edits that are later discarded. background 0.52 0.17 0.02 asserted 1.00
Second, the signals available before retraining are unreliable: sampled training losses can look solved while full-ranking performance remains poor, and they are not comparable across edits that change the loss or sampler. background 0.56 0.30 0.02 asserted 0.97
We propose RecRSI, which generates diverse candidate edits from a diagnosis of the current model and selects one for full retraining using early ranking feedback: each candidate receives a short trial, the first steps of its full training run, scored by full-ranking NDCG@10 on held-out probe users. method 0.89 0.94 0.11 asserted 0.99
With two sequential recommenders on three datasets and the same number of full retrainings, RecRSI significantly outperforms existing self-evolving agents in every setting, and on both Amazon datasets reaches in its first round a ranking quality that none of them reaches in five. result 1.00 0.96 0.91 asserted 1.00

What kind of paper the classifier reports this is: method or tool 1.00 · evidence from observation or experiment 0.97

What was examined, and what was not

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How the labels were made

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Figures (6)
Figure 1 of the paper
Figure 1. Why self-improving recommenders need a signal before the retraining. (a) Ranking feedback arrives only after a full
Figure 2 of the paper
Figure 2. The evolution loop of RecRSI (left) and its short-trial step on the running example (right). In each round, RecRSI (1)
Figure 3 of the paper
Figure 3. Quality and risk of the signals that choose among
Figure 4 of the paper
Figure 4. Select NDCG@10 vs. cumulative GPU time (SASRec;
Figure 5 of the paper
Figure 5. What the short trials reveal in the 20 rounds of
Figure 6 of the paper
Figure 6. Every round of every method on LastFM (one full retraining per round). Top: select NDCG@10 of the retained model

Figures are the authors', reproduced from the paper.

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