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Under review as a conference paper at ICLR 2027

User History Reveals Residual Preference in Recommender Candidate Distributions

Abstract

User histories can distinguish preferences among recommendation candidates that receive the same observed feedback, yet these distinctions may remain only partially expressed in a trained model's output. We study this residual user preference through history-guided refinement of a frozen candidate distribution under explicit probability-preservation constraints. We introduce \bench, a controlled benchmark combining real item catalogs from seven domains with programmatic user trajectories, private candidate-level utilities, and shared catalog features for generation and history scoring. We propose Selective Mass-Preserving History Projection (\method), which uses candidate-discriminative history scores to refine the teacher's conditional distribution within an eligible subset without additional policy training. The update preserves the subset's total probability mass and every outside-set probability, with exact recovery of the teacher distribution when intervention is rejected. Under the benchmark's feedback-conditioned protocol, \method improves GRPO's mean expected utility by on Test-IID and on Test-OOD relative to the frozen teacher. Across four teacher configurations, all 44 evaluated held-out domain–teacher–split cells have positive lower bounds in their pointwise 95% bootstrap intervals for the cluster-mean gain. In pooled diagnostics spanning Validation and both test splits, substituting another user's history reverses the mean gain from to , connecting the improvement to user-specific historical evidence. These controlled results demonstrate recoverable preference in frozen recommendation distributions and, through comparison with unconstrained updates, reveal the utility cost of preserving designated candidate probabilities. Anonymous artifacts: https://anonymous.4open.science/r/ICLR_smphp-4C3D/.

Primary area:
datasets and benchmarks
Keywords:
recommender systems, user history, residual preference, inference-time refinement, preference optimization, probability-preserving projection, personalized recommendation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

This paper introduces the concept of residual user preference and accordingly proposes the framework of SMPHP, which improves the recommendation scores given by frozen teachers by using user history. Extensive experiments are conducted to show the validity of the framework. A benchmark is also produced for similar tasks.

Critical strengths

I like the idea of utilizing the user history to calibrate some parts of the frozen teachers’ recommendation scores and improve the expected utilities.

Experiment section is thorough. It looks persuasive to me that the framework SMPHP is useful in real datasets.

Critical weaknesses

The problem and model look well-defined, but there seems to be no theoretical guarantee to support that the proposed framework will always (or under some assumptions) yield better results than frozen teachers. For example, how do we make the RHS of equation (12) positive? What are equivalent conditions? I read that you admitted in section 6 that ``We do not claim ... that every accepted edit improves utility.’’ What are the conditions under which your framework is superior? If this is not specified, I think the significance of this work will be compromised.

Section 3.1 could be more clear. For example, many letters are introduced and defined without even specifying what they are.

Label of y-axis in the first plot of Figure 2 lies out of margin.

The README in the code repo is in Chinese.

Questions for authors

Q1. I was reading section C.2 and I’m a bit confused by how you define the metrics. The word ``utility’’ looks like an abstract metric, unlike metrics such as accuracy, F1, etc. You defined utility in equation (3), but how does that reflect the objective power of models in real datasets? It gives me the feeling that you shoot an arrow first and then draw the target. Maybe I missed something but please clarify that.

5 comments

Response to Reviewer WQGP

We thank the reviewer for the careful reading and for the encouraging comments on the idea and the experiments. We answer Q1, W1 and W2–W4 in order.

Q1. Why expected utility instead of accuracy or F1? Is it "shooting the arrow first and drawing the target later"?

Why not accuracy or F1. In one display of 8 candidates the user usually clicks one; the other 7 all have feedback 0. SMPHP keeps the protected candidate fixed and moves probability among the others, for example from a disliked item to a liked one. Accuracy and F1 do not change, because the clicked item has not changed. Measuring this needs a utility for every candidate, so we use expected utility EU(p)=∑ipiUi\mathrm{EU}(p)=\sum_i p_iU_i. EU is a simulator quantity, not a click rate or revenue.

The target is drawn before the arrow. The simulator computes each candidate's utility UiU_i from nine components of the user state (Appendix A.3) before SMPHP is run, and stores it in a private file. At test time SMPHP sees only public item features, the teacher distribution and the user's history. Validation utilities are used only to choose the gate threshold.

If the metric favored our method, changing the input should not matter. It does:

  • Replacing the user's history with another user's history: gain goes from +0.01997 to −0.01299 (§5.3).
  • Replacing the history direction with a uniform one: −0.03082 (Table 3).
  • Shortening the history lowers the gain steadily: 20 events +0.01995, 10 events +0.01915, 5 events +0.01761 (Table 13).

Standard ranking metrics agree. We take the candidate with the highest utility as the relevant item and compute HR, NDCG and MRR. These use only which candidate is best, not the utility values. On 132 held-out units (Appendix J):

MetricMean changeUnits where it improves
HR@1+5.19 pp132/132
NDCG@3+7.90 pp132/132
MRR+5.71 pp132/132

The Spearman correlation between ΔEU and ΔHR@1 across units is 0.536, and with ΔMRR 0.629.

On real data EU cannot be computed, because logs do not record the utility of items the user did not choose. On ReRe's public data we report NDCG@10 with paired intervals: the intervals exclude zero in the three domains where the gate activates, and on Yelp the gate never activates and returns the teacher unchanged. We do not claim online gains (§6).

W1. When is the RHS of Eq. (12) positive? (Eq. (13) in the revision)

Exact condition. Let d=q⋅∣EH−p⋅∣Etead=q^H_{\cdot|E}-p^{\mathrm{tea}}_{\cdot|E} be the change of distribution inside the adjustable set EE, and AH=⟨d,UE⟩A_H=\langle d,U_E\rangle. Then ΔEU=ρ ME AH\Delta\mathrm{EU}=\rho\,M_E\,A_H. Since ρ≥0\rho\ge0 and ME≥0M_E\ge0, ΔEU>0\Delta\mathrm{EU}>0 if and only if ρ>0\rho>0, ME>0M_E>0 and AH>0A_H>0. In words, the history distribution must give higher expected utility than the teacher distribution inside EE.

New Appendix M gives five propositions with short proofs:

  1. The sign condition above.
  2. AHA_H does not change if a constant is added to all utilities.
  3. ΔEU is linear in ρ\rho, so there is no overshoot.
  4. Sufficient condition: if for every pair i,j∈Ei,j\in E, (di−dj)(Ui−Uj)≥0(d_i-d_j)(U_i-U_j)\ge0, then AH≥0A_H\ge0. The history does not need to order every pair correctly; errors on pairs with small utility differences cost little.
  5. Bound in any case: ∣ΔEU∣≤ρmax⁡ rangeE(U)|\Delta\mathrm{EU}|\le\rho_{\max}\,\mathrm{range}_E(U), so one edit can lose at most one fifth of the utility range inside EE.

Checks. The identity holds on all 178,200 events (maximum error 8.36×10⁻¹⁶); linearity in ρ\rho gives R2=1.0R^2=1.0; the bound is never violated on 118,800 test events. Grouping test events by the utility range inside EE, the share with AH>0A_H>0 rises from 0.707 (smallest range) to 0.930 (largest), while the mean |ΔEU| rises from 0.0069 to 0.0406, as Proposition 4 predicts.

The gate. At test time UiU_i is unknown, so no method can guarantee AH>0A_H>0 for every event. The gate estimates it from history agreement and concentration: precision 0.879 and recall 0.930 for the sign of AHA_H, with mean AHA_H 0.282 on accepted events and 0.055 on rejected ones (Appendix J). Recalibrating the threshold on Validation lowers the share of harmful accepted edits for GRPO from 25.1% to 17.9% and the worst-5% loss from −0.0323 to −0.0118 (Table 11).

W2–W4. Presentation

  • §3.1 now defines every symbol before use. Renamed symbols: history length TuT_u, teacher pteap^{\mathrm{tea}}, gate confidence zz, final distribution pfinp^{\mathrm{fin}}.
  • Figure 2(a): the y-axis label is now inside the margin.
  • README: the anonymous repository now has an English README with the directory layout, environment, data generation and commands for every table.

2026-11-9-rebuttal-R3-WQGP-PART2

1.2 Second, why is this not "shooting the arrow first and then drawing the target"? (using the analogy of "the target, the gun and the bullet")

Let us borrow the analogy of archery and target shooting:

  • The "target" (the private candidate utilities UiU_i) was set up before the shot and locked in a safe. In the data-construction stage, the simulator computes the true utility UiU_i of every candidate from 9 components (Eq. (3) in Section 3.2 and Appendix A.3), namely the user's long-term profile, recent state, session goal, negative aversion, novelty, repetition and popularity. The error between the sum of the 9 components and the stored utility is within 1.01×10−61.01\times10^{-6}. These utilities are sealed separately in a private evaluation file. The target was generated before SMPHP existed; it was fixed before SMPHP existed.

  • The "gun" (the SMPHP algorithm) cannot see the "target" UiU_i when it fires. At test time SMPHP sees only the public candidate item features, the output of the frozen teacher pteap^{\mathrm{tea}}, and the "bullet", i.e., the current user's interaction log HuH_u. The public observations and the private utilities are stored in different files and are linked only by the sample ID. The utilities of the test set never enter inference. The utilities of the validation set are used for one thing only: choosing the gate threshold. This is the same practice as ordinary validation-set tuning.

  • The most direct counter-evidence: the "history swap" experiment (Figure 2c). If the target UiU_i had been drawn to match the gun that is SMPHP, then this gun should hit regardless of which bullet is loaded. We ran a counterfactual experiment in Section 5.3 (Figure 2c): the frozen teacher, the candidate slate, the sealed target UiU_i and the SMPHP algorithm (the gun) are all held fixed, and only the "bullet" loaded into the gun is replaced by another user's history. As a result, the mean utility gain changes from +0.01997+0.01997 to −0.01299-0.01299, turning from positive to negative. Likewise, if the history direction is replaced by an uninformative uniform distribution (the Uniform direction in Table 3), the utility drops by 0.030820.03082. Only when the current user's own history (the matching bullet) is loaded into SMPHP (the gun) can the pre-sealed utility (the target) be hit; load the wrong bullet and the shot misses. This shows that the gain comes from the user's own history, not from a metric that favours our method.

  • What the bullet is loaded with also matters. Besides "swapping in someone else's bullet", we also checked what happens when "the same bullet is damaged" (Table 13, 126 diagnostic units):

Treatment of the historyΔEU
Full history+0.01997
Keep only the most recent 20 events+0.01995
Keep only the most recent 10 events+0.01915
Keep only the most recent 5 events+0.01761
Keep only 0 / 1 / 3 events (below the gate lower bound, forced fallback)0
Shuffle behavior types (the correspondence of click, save, reject, etc.)+0.01436
Shuffle timestamps+0.01848
Use only the most recent 3 days+0.00079
Replace with another user's history−0.01299

The gain varies with the content of the history: the shorter and the noisier the history, the smaller the gain; after the behavior types are shuffled the gain falls by about 28%. If the target had been drawn to match the gun, these modifications of the history content should not produce such a regular pattern.

2026-11-9-rebuttal-R3-WQGP-PART3

1.3 Third, the conclusion holds equally if we do not use the continuous EU metric at all and look only at hard metrics such as the ranking and Top-1

To remove your concern about the numerical scale of the continuous utility, we switched to an evaluation that does not use the utility values at all: we treat the candidate slate as an ordinary ranking task, define the relevant item as the candidate with the highest true utility (using only the information "which one is best", not the size of the utility), then rank by probability and compute HR, NDCG and MRR. Any monotone transform of the utilities (for example squaring all of them, multiplying by 100, or taking logarithms) leaves these metrics unchanged, so they cannot be "inflated" by the scale of the utility.

Table Q1-a: change in ranking metrics over 132 test units (SFT and GRPO with 7 domains each, ReRe and TAWin with 4 domains each, 3 seeds per domain, two test sets Test-IID and Test-OOD)

MetricMean changeShare of units with ΔEU>0 in which this metric also improves
HR@1+5.19 percentage points132 / 132
HR@3+9.66 percentage points132 / 132
NDCG@1+5.19 percentage points132 / 132
NDCG@3+7.90 percentage points132 / 132
NDCG@5+6.91 percentage points132 / 132
MRR+5.71 percentage points132 / 132

HR@1 is the most conservative of these metrics, meaning "is the best candidate placed first". It rises by 5.19 percentage points on average.

Table Q1-b: correlation between EU and common ranking metrics (132 units)

ComparisonSpearman correlation
EU of the teacher vs. NDCG@10.856
EU of the teacher vs. NDCG@30.869
EU of the teacher vs. NDCG@50.854
ΔEU vs. ΔHR@10.536 (p=3.7×10−11p=3.7\times10^{-11})
ΔEU vs. ΔNDCG@50.818
ΔEU vs. ΔMRR0.629

All correlations are positive, and p<10−8p<10^{-8}. This shows that EU and the common ranking metrics measure the same thing. EU is finer, because it can also see the movement of probability between candidates when the ranking does not change, which is exactly the phenomenon this paper studies.

In addition, the paper already contains two Top-1 results that do not depend on utility weighting, consistent with the above:

  • The probability received by the best candidate (Table 8). Looking only at the single item with the highest true utility in the slate (arg⁡max⁡iUi\arg\max_iU_i), after adding SMPHP the probability that the four teacher models assign to it increases on the test sets: GRPO +0.01493+0.01493, SFT +0.01730+0.01730, ReRe +0.02157+0.02157, TAWin +0.02135+0.02135.
  • The correction win rate of the deterministic Top-1 recommendation (Appendix E.3). If the system finally recommends only 1 item (taking arg⁡max⁡ipi\arg\max_ip_i), then on Test-IID the number of times SMPHP turns a wrongly ranked Top-1 into a correct one is 8.8 times (GRPO), 8.6 times (SFT), 10.8 times (ReRe) and 8.0 times (TAWin) the number of times it turns a correct one into a wrong one. The corresponding mean Top-1 utility gains are +0.0254, +0.0407, +0.0847 and +0.0881. Cases where it gets things wrong also exist, and their share is not zero, which is consistent with the later conclusion that "not every adjustment is guaranteed to be positive".

So the conclusion is the same whether we measure with expected utility EU or with such common metrics as Top-1 hits, correction win rates, NDCG and MRR.

Reviewer_W4aUOpenReview ↗
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Paper summary

This paper asks whether a frozen recommender's candidate distribution still contains recoverable, user-specific residual preference usable at inference time without retraining. The authors introduce BehaviorTie-Bench, a controlled benchmark combining real catalogs from seven domains with programmatic user trajectories and private candidate-level utilities, and propose SMPHP, an inference-time layer that mixes teacher and history conditionals only within an eligible set while exactly preserving outside-set probabilities, eligible-set mass, and falling back to the teacher when the gate rejects. With LoRA-tuned Qwen2.5-1.5B teachers, SMPHP improves expected utility for all 44 held-out domain-teacher-split cells (e.g., GRPO +5.0% IID, +5.9% OOD), while a history swap reverses the gain; boundary checks show the effect weakens under independent encoders and unfiltered splits.

Critical strengths

The method has exact, checkable structural guarantees. The update in Eq. (8) leaves outside-set probabilities equal to the teacher's, preserves eligible-set mass, and returns the teacher exactly when rho = 0 (Eqs. 10-11, verified to machine precision in Table 14). Eq. (12) further decomposes the utility change into eligible mass, intervention strength, and the history conditional's advantage, making the effect interpretable and its failure modes predictable. This matters because it distinguishes SMPHP from ad-hoc reranking: preservation and fallback are guaranteed rather than hoped for.

Critical weaknesses
  1. The practical necessity and cost of the preservation constraint are not fully established. The paper motivates preserving outside-set probabilities and eligible-set mass, but does not identify a concrete deployment where this is a hard requirement. In the pooled diagnostic including Validation, unconstrained Naive History obtains +0.05456 versus +0.01997 for SMPHP while violating protected probabilities and eligible-set mass (Table 4), so the constraint discards a large fraction of the benchmark gain; the public fixed-candidate check shows only 10^-5 to 10^-4 NDCG@10 changes without paired intervals. This does not invalidate the constrained objective, but the paper should justify why this boundary is the relevant one and what it buys in practice.

  2. Evidence for transfer beyond the authors' constructed alignment is limited. The generator and primary scorer share NMF features, and slices use Oracle/structural selection. The paper's own sensitivity checks show attenuation: the GRPO gain falls to +0.00116 / -0.00094 under independent title encoders (Table 10), although other teachers retain larger gains; the unfiltered split retains 59% / 52% (Table 11). Thus the controlled gain is real under the declared condition, but end-to-end utility transfer under independent representations and real-user data remains unestablished. The paper should temper any practical claim accordingly or provide stronger evidence.

Questions for authors
  1. The paper motivates the probability-preservation constraint narratively, but I could not identify a concrete deployment scenario where such a constraint actually binds. Could the authors describe a real or realistic recommender setting in which protecting outside-set probabilities and eligible-set mass is a hard requirement, and what the system would lose without it?

  2. Do the authors intend the claim to be conditional on the shared NMF representation and constructed slices? If they intend a practical recommendation-layer claim, what evidence beyond the current sensitivity checks supports retention under independent encoders or real data? If not, the paper should state this scope explicitly in the abstract and introduction.

6 comments

Response to Reviewer W4aU

We thank the reviewer for the careful reading and for recognizing the exact structural guarantees of SMPHP and the interpretability of Eq. (12) (Eq. (13) in the revision). We answer the two questions in order.

Q1. Where does the preservation constraint actually bind, and what does it cost?

Deployment settings. SMPHP works at the re-ranking stage, after fine ranking. In industrial systems this stage often cannot rewrite the whole distribution, because other parts of the system already rely on some of the probabilities. We added these settings to §4 and Appendix K:

  1. Contracted exposure. Promoted slots, brand contracts and operator-inserted items must receive an agreed exposure share. Lowering their probability breaks the contract.
  2. Audit and compliance. For must-show or age/region-restricted items, auditors check that the probability equals the audited value. "Almost unchanged" does not pass.
  3. Off-policy evaluation. IPS, SNIPS and DR are valid only if the logged probability equals the probability actually used. If a later layer silently changes it, every evaluation based on those logs is biased.
  4. Exploration traffic. Probability reserved for new or long-tail items produces the training data for the next model. Moving it to exploitation shrinks and biases that data.
  5. Explicit negative feedback. An item the user marked "not interested" must not be pushed back up just because it is similar to a liked item.

In SMPHP, protected candidates PP and negative-feedback candidates NN are outside the adjustable set EE and keep their probabilities exactly. The total probability of EE is preserved, and the method returns the teacher output exactly when the gate rejects. If none of these settings applies, the unconstrained update is the better choice, and we now say so in the paper.

The cost of the constraint. Naive History uses the same history without the constraint. We now present it as the unconstrained reference that measures the cost of the constraint, not as a competing method. Table 4 and Table 14 (126 SFT/GRPO units, including Validation):

MethodΔEUAnchor driftOutside-E driftMass errorΔEU when gate rejects
Naive History+0.054562.15×10⁻²5.51×10⁻³1.21×10⁻²1.44×10⁻²
SMPHP+0.019971.34×10⁻¹⁸5.20×10⁻¹⁹5.14×10⁻¹⁷2.74×10⁻¹⁸

The constraint costs 63.4% of the unconstrained gain (1 − 0.01997/0.05456). We now report this number in the main text. In the settings above, Naive History's drifts mean the requirement is violated, whatever its utility gain.

Paired intervals on public data. We added user-clustered paired bootstrap intervals for ΔNDCG@10 (20,000 resamples, same candidates and teacher):

DomainΔNDCG@1095% paired intervalGate activation
Industrial+4.96×10⁻⁵[7.3×10⁻⁶, 1.04×10⁻⁴]0.979
Office+1.29×10⁻⁴[1.84×10⁻⁵, 2.74×10⁻⁴]0.994
Toys+1.51×10⁻⁴[8.1×10⁻⁵, 2.31×10⁻⁴]0.994
Yelp0 (gate never activates)—0.000

The intervals exclude zero in the three domains where the gate activates. The values are small because the target item is in the 10 candidates in only 0.26%, 0.60%, 0.28% and 0% of events; otherwise no reranking can change NDCG. We now describe this check only as evidence that SMPHP behaves as designed, not as a ranking improvement.

Q2. Is the claim conditional on shared NMF and constructed slices?

Yes. The claim holds under the benchmark's declared conditions: a frozen teacher, 8 fixed candidates, simulated utilities, and a history scorer that shares 32-dimensional catalog features with the generator. This scope is now stated in §4.6 and §5.6. We do not claim gains under arbitrary representations or with real users.

Independent encoders. We added three stronger title encoders (Table 9, Test-IID, GRPO):

RepresentationShared NMFMiniLMBGE-M3E5-large-v2 (new)GTE-large (new)Qwen3-Emb-0.6B (new)Random
ΔEU+0.01895+0.00116−0.00094−0.00746−0.00652−0.00292−0.00658
Probe0.5580.2870.2690.2910.3210.2880.086

The probe (Spearman correlation between history scores and true utility) stays well above random, so the information is still there. It does not turn into gain because these encoders place the 8 titles of one list very close together, so the history direction becomes nearly uniform and the gate blocks most edits. Larger encoders do not solve this.

Unfiltered split. Without slice filtering, the gain is smaller but stays positive for all four teachers, retaining 59.3%/52.4% (GRPO), 60.4%/53.2% (SFT), 67.1%/59.3% (ReRe) and 68.8%/59.8% (TAWin) on IID/OOD (Table 10). Filtering amplifies the effect but does not create it. This split still comes from the same simulator, so it tests dependence on filtering, not transfer to real users.

2026-11-9-rebuttal-R2-W4aU-PART1

We thank the reviewer very much for the careful reading and detailed evaluation of this paper. We are especially grateful for the recognition of SMPHP's structural guarantees, and for the positive assessment of the interpretability of Eq. (13).

The two questions you raise are very important: **first, under what circumstances the strict probability-preservation constraint is genuinely necessary, and whether this constraint is worth the utility cost it brings; second, whether the currently observed gains depend too heavily on the construction conditions of BehaviorTie-Bench, especially the shared NMF representation and the mechanism-slice selection.

1.1 Very small NDCG changes on public data

The reviewer points out that the NDCG@10 changes we previously reported lie only on the order of 10−510^{-5} to 10−410^{-4}, and that no paired confidence interval was given. This makes these changes hard to interpret statistically in a meaningful way. This criticism is correct. We additionally performed a paired bootstrap clustered by user (20,000 resamples), with the candidate set and the teacher unchanged:

Data domainΔNDCG@1095% paired intervalGate activation rate
Industrial+4.96×10−5+4.96\times10^{-5}[7.0×10−6, 1.04×10−4][7.0\times10^{-6},\ 1.04\times10^{-4}]0.979
Office+1.29×10−4+1.29\times10^{-4}[1.8×10−5, 2.74×10−4][1.8\times10^{-5},\ 2.74\times10^{-4}]0.994
Toys+1.50×10−4+1.50\times10^{-4}[8.1×10−5, 2.31×10−4][8.1\times10^{-5},\ 2.31\times10^{-4}]0.994
Yelp0[0, 0][0,\ 0]0.000
In the three domains with activations, none of the intervals contains 0. In Yelp the gate did not activate and the teacher distribution is returned directly, which is the fallback guarantee of Eq. (12).

Why the numbers are so small: in this public protocol, the proportion of events whose evaluation target appears in the candidate set is only 0.26% (Industrial), 0.60% (Office), 0.28% (Toys) and 0% (Yelp). If the target is not in the candidate set, no reranking can change NDCG, so more than 99% of the events have a change identically equal to 0. Looking only at the events whose target is in the candidate set, ΔNDCG@10 is +0.0150, +0.0232 and +0.0572 respectively. However, these three subsets contain only 33, 81 and 111 events, so we treat them as diagnostics only, not as ranking results.

The conclusion is tightened accordingly: on public fixed candidate sets that do not use the current feedback, SMPHP carries out the constrained update as expected, and falls back exactly when the gate rejects. We no longer use these numbers to claim how large the actual ranking improvement is.

2. W2 / Q2: Do the gains depend on the alignment built into the construction? Can they transfer?

Yes, our conclusions have preconditions, and the preconditions are exactly the conditions declared by BehaviorTie-Bench. What this paper can show is: under these conditions, the frozen model's output still contains preferences that can be recovered from user history. We cannot show that SMPHP stably improves utility under arbitrary representations or in real user environments. These conditions are: a frozen teacher, a fixed slate of 8 candidates, simulated utility, and a history scorer that shares 32-dimensional catalog features with the data generator. Among them, the shared catalog features were already stated in the original paper: Section 3.2 (constructing the user-behavior dataset) states that the history scorer and the data generator share the 32-dimensional catalog features, the information-boundary section delimits which information can enter inference, and Section 5.6 reports the encoder results. This revision only states this condition more explicitly: it is made explicit in Section 4.6 (Scope) and Section 5.6; the abstract and the introduction are left unchanged.

2.2 How each of the three components is validated

This paper has three components: the dataset BehaviorTie-Bench, the method SMPHP, and the proof of the source of the gain, Eq. (13). They are validated in different ways.

Dataset: corrupting the user's recommendation history as a control, to verify that the gain comes from the current user's history rather than from the shared features leaking the answer directly.

This dataset is needed because an ordinary log records only the items the user actually touched or chose, and does not provide the utility of the other candidates in the same list, so one cannot compute how much a probability reallocation actually improved the user's outcome. BehaviorTie-Bench makes this measurable with seven real item catalogs, programmatically generated user trajectories, a fixed slate of 8 candidates and private candidate-level utilities. The item catalogs are real; the user trajectories and utilities are simulated; EU is the expected utility inside the simulator, not click-through rate or conversion rate.

The shared 32-dimensional features are the public description of an item (TF-IDF on title and category, then NMF); they tell the scorer where an item sits, not which direction this user prefers. Test-set private utilities do not enter inference; validation-set utilities are used only to select the gate threshold. Of course, isolating the utilities alone cannot automatically remove all the conveniences brought by the construction, so we use three controls to check whether the gain really depends on the current user's history:

  • Swapping in another user's history: the representation is unchanged, only the history no longer matches the user, and the gain goes from +0.01997 to −0.01299 (Section 5.3).
  • Same shared features, different mechanism slice: the gain on the Clean Tie Ambiguous slice is only +0.00008 (Figure 2b). With the same representation, when the history contains no information that can distinguish the candidates, the method has no effect.
  • Swapping in a random representation: GRPO and SFT become −0.00658 and −0.00303. ReRe and TAWin still have +0.00755 and +0.00691, showing that on these two teachers, redistribution inside the eligible set itself also contributes part of the gain, which we do not credit entirely to history information.## 2026-11-9-rebuttal-R2-W4aU-PART5

Conclusion: under the declared conditions, the gain is indeed related to the current user's history; but this does not yet show that the gain is independent of the simulator and the shared representation, which requires Section 2.3 to remove the construction conditions one by one.

Method: fix the shell and change only the direction, to verify that SMPHP's scorer is better than simple directions and common history models. In Table 3, removing any one component lowers utility; in the newly added matched-shell comparison, EASE, ItemKNN and MF-ALS are all worse than SMPHP (see our reply to reviewer j3Xf).

Proof: verify what determines the sign of the gain. Eq. (13) gives ΔEU=ρMEAH\Delta\mathrm{EU}=\rho M_E A^H. When ρ>0\rho>0 and ME>0M_E>0, ΔEU>0\Delta\mathrm{EU}>0 if and only if AH>0A^H>0: only when the history distribution is better than the teacher distribution in true utility does this update bring a gain. This explains both why the method can work and under what circumstances it fails, for example when the history is wrong, the representation is unsuitable, or the candidates cannot be separated. This identity holds event by event on 178,200 events, with a maximum error of 8.4×10−168.4\times10^{-16} (see our reply to reviewer WQGP).

It must be emphasized that this is not equivalent to "every accepted update makes things better". The gate cannot see the test-set utility, and the original manuscript also shows that under the fixed gate about a quarter of the accepted updates are negative. So SMPHP's theoretical contribution is a strict feasible-region guarantee plus a testable gain condition, not an unconditional improvement theorem.

2.3 Your concern: two design choices in the construction may give the method an advance advantage

Table 10 of the submitted version (now Table 9 of the revised paper) already showed the method's performance drop under independent representations, but did not distinguish the two possible causes of this drop.

And this distinction directly affects how readers should understand the experimental conclusions.

Hypothesis H1: Information Leakage

The method obtains a utility gain only because the history scorer and the generator share the same feature representation.

Once an independent representation is used, the relevant preference information does not actually exist.

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Paper summary

This paper studies whether user-specific preferences not fully captured by a pre-trained recommender can be recovered through history-guided redistribution of candidate probabilities.
It introduces BehaviorTie-Bench, a controlled benchmark with oracle candidate-level utilities, and proposes SMPHP which is an inference-time refinement method that preserves designated probabilities and total probability mass.

Critical strengths
  1. Controlled evaluation with oracle utilities
  • The proposed BehaviorTie-Bench provides candidate-level ground-truth utility, enabling direct evaluation of whether history-based refinement improves expected utility or not, and analysis of the mechanisms underlying its gains.
Critical weaknesses
  1. Insufficient comparison against existing approaches
  • OBSERVED-FEEDBACK AMBIGUITY is a well-investigated problem in recommendation.
  • For example, propensity-based and doubly robust estimators, including Doubly Calibrated Estimator for Recommendation on Data Missing Not At Random [WWW'24], have already studied this ambiguity problem.
  • Also, rating generation works, including Rating augmentation with generative adversarial networks towards accurate collaborative filtering [WWW'19], have investigated how to perform user-aware rating imputation. It is unclear whether SMPHP recovers genuinely additional preference information or simply performs a second round of preference estimation/reranking.
  • Strong comparisons with these alternatives are needed to establish the method’s novelty and incremental value.
  1. Notations are not solid
  • In lines166-171, what is b and x?
  • Also, T for H_u and T for p_i are different. why?
  • Waht is p^F in Eq.3?
Questions for authors

Please refer to weaknesses.

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

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