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Under review as a conference paper at ICLR 2027

Diffusion-Based Data-Driven Assortment Optimization

Abstract

Assortment optimization is a fundamental problem in revenue management, typically addressed using parametric choice models such as the multinomial logit (MNL) and its variants. While these models enable tractable formulations, their performance is sensitive to model misspecification and often struggles to capture complex customer behavior. In this paper, we propose a model-agnostic framework for assortment optimization based on guided discrete diffusion. We represent assortments as binary vectors and perform stochastic search via a learned reverse diffusion process, avoiding explicit combinatorial enumeration. To incorporate decision objectives, we introduce a reward-guided mechanism that biases local transitions using estimates of expected revenue. This allows the method to effectively balance exploration and exploitation during generation. Empirically, we show that the proposed approach consistently identifies high-quality assortments and remains robust under model misspecification, often recovering near-optimal solutions in high-dimensional settings. Moreover, the generative nature of diffusion enables the production of diverse high-performing assortments, offering flexibility beyond a single deterministic solution. These results highlight the potential of generative modeling as a scalable and robust paradigm for combinatorial optimization in data-driven decision-making.

Primary area:
optimization
Keywords:
Assortment optimization, Diffusion model, Guided diffuision

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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

D3AO addresses offline assortment optimization by combining a neural choice estimator, a plug-in revenue function, and a binary denoising model trained on historical assortments. During generation, coordinate-wise revenue differences modify the reverse proposal's Bernoulli logits, with stronger guidance toward the final steps. The paper interprets the guidance as a KL-regularized improvement for a local additive surrogate. Synthetic experiments use MNL, MCCM, and MMNL choice models, up to 100 products, and 256 generated candidates per instance. Additional analyses cover exact recovery, diversity, sample size, and changes in the assortment-collection policy.

Critical strengths
  1. Choice estimation, a historical assortment prior, and coordinate-wise guidance have clearly separated roles. Theorem 2 gives an exact interpretation of the logit shift for its local surrogate. The unguided comparison also establishes that the revenue signal is important in the tested setting.

  2. The method performs strongly on the synthetic MMNL benchmark relative to the misspecified parametric baselines. Reporting means, quantiles, recovery, and diversity is more informative than reporting only the best candidate, and the distribution-shift experiment exposes an important limitation rather than hiding it.

Critical weaknesses
  1. Comparisons with MNL-MLE and MCCM-EM change both the choice estimator and the optimizer. Improvements under MMNL misspecification can therefore arise from the neural estimator alone. The unguided ablation establishes the need for guidance, not for a learned diffusion prior. This distinction is especially important because Section 4.1 replaces the standard reverse kernel with direct clean-sample resampling, while the reported maximum guidance strength is 1000. A comparison using the same fitted GAsN/RAsN revenue function with non-diffusion search, under comparable evaluation and time budgets, is needed to substantiate the central contribution.

  2. The maximum true-revenue ratio among 256 candidates is a valid oracle statistic, but the learner cannot use true revenue to choose that candidate at deployment. The performance of the candidate selected by estimated revenue is not clearly reported. This omission becomes decisive under collection-policy shift: in Table 9, MMNL with N=80 gives a GAsN candidate mean of 55.18% despite an oracle maximum of 91.34%; the RAsN maximum is 80.36%. The Boltzmann assumption based on true revenue is a controlled benchmark choice, not a consequence of Theorem 1 about actual historical policies. Moreover, the abstract's pessimistic-estimation language lacks a corresponding uncertainty penalty or confidence bound in the method. Together, these issues leave the claimed offline improvement insufficiently supported outside the main data regime.

Questions for authors
  1. With exactly the same fitted GAsN/RAsN revenue model, how does D3AO compare with multi-start discrete local search or another non-diffusion optimizer at matched evaluation budgets? How sensitive are the results to guidance strength, and does the learned prior improve over reward-guided search from an untrained or simple reference proposal?
  2. What is the actual final selection rule? Please report the true revenue of the candidate maximizing estimated revenue, alongside the oracle maximum, especially in Table 9. Is any uncertainty-aware pessimistic adjustment implemented?
  3. How are product revenues generated, Boltzmann assortments sampled for large N, and MMNL reference optima computed or certified? Please also explain why favored-item utility means grow with N, and diagnose Table 8's N=40 GAsN mean decline from 97.77% at 10,000 observations to 73.81% at 50,000. Does this originate in estimation, prior learning, or optimization?
1 comment

We thank the reviewer for the careful assessment and the detailed numerical checks. New tables R1–R3 are in our reply to Reviewer yEcx; all new results use 10 seeds, the paper's hyperparameters and true optimal ratios (%).

W1. Confounded baselines, learned prior, guidance sensitivity

We agree that MNL-MLE and MCCM-EM change both estimator and optimizer, and that the unguided ablation does not test the prior. With the identical fitted GAsN/RAsN reward:

(a) Direct optimization (Table R2). Multi-start local search (add/drop), simulated annealing and random search, each with D3AO's number of R^θ\widehat R_\theta evaluations, for N∈{40,80,120}N\in\lbrace 40,80,120\rbrace and several budgets. Local search and SA match D3AO or are slightly better (up to ~0.5 points at N=120N=120), already at 1/16 of the budget. We no longer claim that diffusion search beats direct optimization of the same reward.

(b) Learned prior (Table R3). Same guidance with the prior versus gϕ=0g_\phi=0. The prior does not improve the returned assortment in any setting (n∈{1,000,3,000,10,000}n\in\lbrace 1{,}000,3{,}000,10{,}000\rbrace, N∈{40,80,120}N\in\lbrace 40,80,120\rbrace, shifted logging); without it, results are equal or slightly better. We state this, and identify reward estimation as the limiting factor on these benchmarks. We did not ablate the reverse kernel of Sec. 4.1; the revision describes it as a design choice and removes the claim that it performs better.

(c) Guidance strength (MMNL, N=80N=80, γ=3\gamma=3). The returned assortment reaches 68.10 ± 5.61% at λmax⁡=10\lambda_{\max}=10, 79.99 ± 5.00% at 100, 97.42 ± 0.97% at 1000 and 97.60 ± 0.74% at 10000: insensitive once λmax⁡≥1000\lambda_{\max}\ge 1000, much worse when guidance is weak. The effective shift λtΔiR^θ\lambda_t\Delta_i\widehat R_\theta depends on the scale of R^θ\widehat R_\theta. All submitted experiments used λmax⁡=1000\lambda_{\max}=1000, γ=3\gamma=3; we did not vary γ\gamma.

We also reran both parametric baselines on the new instances (Table R1). They are near-optimal when correctly specified, fall to ~50% under MMNL with Boltzmann data (D3AO 97.13%), and under shifted logging MCCM-EM (97.89%) is slightly better than D3AO (97.20%).

W2. Deployable selection, distribution shift, "pessimistic"

We agree that the oracle maximum cannot be deployed and that the gap matters under shift. The returned decision is now arg⁡max⁡s∈CR^θ(s)\arg\max_{s\in\mathcal C}\widehat R_\theta(s) over distinct candidates. Under shifted logging (uniform size, then a uniform random subset; MMNL, N=80N=80) it reaches 97.20 ± 0.94% versus the oracle 98.73 ± 0.77%, a gap of ~1.5 points (Table R1). These shifted-policy results were obtained by re-running this setting with the hyperparameters stated in the paper (λmax⁡=1000\lambda_{\max}=1000, γ=3\gamma=3); we will update Table 9 with these reruns in the revision.

The Boltzmann policy is a controlled benchmark choice, not a consequence of Theorem 1; we revise Sec. 2.1. "Pessimistic" was inaccurate (plug-in estimate, no uncertainty penalty); we correct the abstract and list uncertainty-aware selection as future work.

Q1 / Q2

See W1(a)–(c) and W2. Selection uses R^θ\widehat R_\theta only; ground truth is used only for evaluation.

Q3. Experimental details and Table 8

  1. Revenues are i.i.d. Uniform(0, 1); no-purchase reward is 0.
  2. Boltzmann sampling is exact by enumeration for N≤20N\le 20; for larger NN, parallel single-site Gibbs (32 chains, 100 burn-in sweeps, thinning 10). Samples are approximate; we do not claim finite-time convergence.
  3. MMNL optima: MILP with a Charnes–Cooper transformation per type, Gurobi with zero MIP gap and required optimal status. All new instances were certified optimal.
  4. MMNL utilities: five equally weighted types; type cc favors a block of N/5N/5 products with utility mean c+N/5c+N/5 (sd 1), others mean −1-1, so heterogeneity grows with NN. We add these details to Appendix A.

Table 8 decline. We re-ran this setting (MMNL, N=40N=40, β0=1\beta_0=1, 10 new instances, statistics over all 256 samples as in the paper). The decline reproduces:

nnGAsN meanRAsN meanReturned (GAsN)
10,00094.67±4.4291.08±7.1794.25±4.66
20,00091.80±6.0290.26±6.4391.25±7.29
50,00077.70±15.2177.24±14.9877.26±15.30

It is not driven by a few runs: the GAsN mean is lower at n=50,000n=50{,}000 than at n=10,000n=10{,}000 on all 10 instances. Optimizing the same fitted R^θ\widehat R_\theta with D3AO, D3AO without the prior, and local search gives exactly the same assortment on every instance and nn. The decline therefore comes from the fitted revenue model (its maximizer has lower true revenue at larger nn), not from the prior or the search. We have not identified why (training hyperparameters were fixed across nn) and will report this as a limitation rather than presenting the sample-size results as monotone.

Reviewer_mU7QOpenReview ↗
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Paper summary

The paper proposed a diffusion-based framework to generate high-quality assortments from historical choice data. In this setting, where the past assortments are generated from a Boltzmann behavior policy, it enables the diffusion learning of better assortments. Synthetic experiments are set up to show the strong empirical performance.

Critical strengths
  1. A new framework for assortment optimization: Based on my previous knowledge, there has been a few deep-learning/first-order frameworks for solving assortment optimization, but the generative model with diffusion is new.
  2. The organization of the paper is clear and makes sense.
Critical weaknesses
  1. The paper's result/analytical foundation is built on the modeling assumption that "the behavior policy is a Boltzmann distribution". This is fine, and I understand it helps establish the sampling distribution analysis in the follow-up theorems. However, a natural question is whether this assumption is valid in the real world, and what type of common assortment generation strategies are included/can be approximately characterized by the Boltzmann distribution. At a minimum, consider a real-world dataset with historical assortments and fit it with the distribution. Similarly, this question remains in the empirical setting where the modeling assumption holds, so it leaves the impression that it would only work under this setting and is not practical enough.

  2. Lack of theoretical results on the optimality guarantees. Comparison with other existing first-order/deep learning frameworks: some of them have shown analytical results to infer the global optimality. This paper claims "nearly optimal" but only empirically demonstrates it, and the experimental setup only tests with the Boltzmann distribution assortment generations. I think it would, in fact, be misleading to state "nearly optimal" in the contribution.

Questions for authors

The question stems from the weakness.

  1. Some literature (that uses first-order or deep learning for combinatorial assortment optimization) is missing or needs a more careful comparison to better understand the paper's contribution: not cited: some give stronger theoretical guarantees.
  • Guo et al. (2025) Solving Assortment Optimization with First-Order Methods and Neural Networks: A Computational Framework and Public Benchmark
  • Li et al. (2025) From Small to Large: A Graph Convolutional Network Approach for Solving Assortment Optimization Problems
  • Yang et al. (2026), Neural Assortment Optimization
  • Dou et al. (2026) Plug-and-Play Guidance for Discrete Diffusion Models via Gradient-Informed Logit Correction
  • Zhu et al. (2026) A Model-free Approach to Assortment Optimization via Local Exploration and Adaptive Projection

cited: whether this paper just applies the below/existing diffusion-based framework to the context of assortment optimization (which is a special case of combinatorial optimization)

  • Sun and Yang (2023) Difusco: Graph-based diffusion solvers for combinatorial optimization
  • Sanokowski et al. (2024) A Diffusion Model Framework for Unsupervised Neural Combinatorial Optimization
  1. Would there be stronger analytical/theoreical results on the optimality guarantees given the Boltzmann distribution behavior policy? As mentioned in the first question, they (e.g.) show nearly optimal solutions for MC choice models (Guo et al. 2025) or generic choice models (Yang et al. 2026) which include the neural choice model used in your setting.

  2. Can you add more examples or empirical justification for the Boltzmann distribution setting?

  • common assortment generation strategies can be included or can be approximately characterized by the Boltzmann distribution
  • a real-world dataset with historical assortments and fit it with the distribution.
  1. Ablation studies:
  • Different assortment generation strategies: What if the historical assortment generation is not Boltzmann
  • Number of historical assortments required to achieve good performance.

I will positively consider raising my evaluation based on the response to the weakness and the questions.

2 comments

We thank the reviewer for the thoughtful review. New tables R1–R3 are in our reply to Reviewer yEcx (10 seeds, paper hyperparameters, true optimal ratios in %).

W1. Validity of the Boltzmann behavior policy

We agree that real logs may come from heuristics, exploration or business rules.

(a) Role of the assumption. Eq. (1) is a theoretical motivation and a controlled benchmark design, not a requirement. Theorem 1 characterizes Boltzmann policies as solutions of entropy-regularized revenue maximization; it does not claim real policies follow it. Neither diffusion training nor guidance requires Boltzmann data: the prior is learned from logged assortments under any policy, and Theorem 2 holds for any reward. We revise Secs. 2.1 and 3.

(b) Non-Boltzmann logging. We ran D3AO on data logged by a policy that draws the assortment size uniformly and then a uniform random subset (MMNL, N=80N=80). The assortment selected by R^θ\widehat R_\theta reaches 97.20 ± 0.94% of the optimum, versus 97.13 ± 1.00% under Boltzmann data (oracle best-of-256: 98.73%). Without the learned prior it reaches 97.48%, so the prior is not what drives performance. Parametric baselines on the same instances reach 96.49% (MNL-MLE) and 97.89% (MCCM-EM): under such broad exploration a misspecified MCCM fit is slightly better than D3AO, whereas under concentrated Boltzmann data both fall to about 50% (Table R1). We did not add further logging policies in this revision.

(c) Real-world validation would need true revenues and logging probabilities, which offline logs lack; we state this as a limitation.

W2. Optimality guarantees

We agree. Near-optimality is an empirical finding on synthetic benchmarks; we replace "near-optimal solutions" with "empirically near-optimal performance on synthetic benchmarks." Theorem 2 shows that the logit-shift guidance exactly solves a KL-regularized local improvement problem under a coordinate-wise reward surrogate. It gives no global convergence or approximation guarantee for the full process, and the simplified reverse kernel is not covered. A comparable guarantee would need assumptions on reward-estimation error, prior accuracy, and the gap between coordinate-wise improvement and global optimization; we add this to a Limitations paragraph.

Q1. Related work and comparison

(a) Guo et al. (2025): first-order method with convergence guarantees for MNL and Markov chain models. Li et al. (2025): graph convolutional framework that transfers from small to large instances. Yang et al. (2026), NAO: continuous extensions and particle-based optimization with near-optimality guarantees under stated conditions. Zhu et al. (2026): model-free, revenue-query-based local exploration with adaptive projection. Unlike these, D3AO learns a generative prior from offline data and guides sampling with an estimated choice model.

(b) Sun and Yang (2023, DIFUSCO), Sanokowski et al. (2024) and Dou et al. (2026, gradient-informed logit correction) are discussed in the revised related work; see also the next question.

(c) We did not run NAO in the rebuttal period. With the same fitted reward and budget, D3AO is comparable to local search and simulated annealing (within ~0.5 points, slightly worse at larger NN), and all are far better than random search (Table R2). We revise our claims: D3AO is a competitive way to optimize a learned revenue model, not better than direct search.

Q. Relationship to DIFUSCO and Sanokowski et al.

D3AO builds on existing discrete diffusion. Unlike DIFUSCO (trained on good solutions) and Sanokowski et al. (explicit objective), offline assortment optimization observes only historical assortment–choice pairs. D3AO therefore (i) estimates revenue with a neural choice model, (ii) trains the prior on logged assortments, not solutions, and (iii) uses coordinate-wise guidance with a KL-regularized interpretation and a schedule that relies less on the reward at highly corrupted states. Our contribution is this formulation, not a new architecture or a guarantee. Our ablation (Table R3) shows that the learned prior does not improve the returned assortment on these benchmarks, and we state this in the paper.

Q2. Guarantees under Boltzmann sampling

The Boltzmann assumption alone does not give global optimality; see W2.

Q3. Practical justification

Boltzmann policies model stochastic selection favoring higher revenue (e.g., noisy or entropy-regularized heuristics); we do not claim practical policies follow it, and D3AO does not require it (W1).

Q4. Behavior-policy and sample-size ablations

Behavior policy: see W1(b). Sample size: Appendix B.4 covers nn from 100 to 50,000, and Table R3 adds n∈{1,000,3,000,10,000}n\in\lbrace 1{,}000, 3{,}000, 10{,}000\rbrace at N=80N=80, where the returned assortment reaches 97.1–97.5%. We re-ran the decline at large nn in Table 8 and traced it to the fitted revenue model (details in our reply to Reviewer Zryf).

Thank you for the clarifications and additional experiments. The revised selection protocol and acknowledgment that near-optimality is empirical address my several concerns. However, my main concern about the methodological contribution remains.

  1. Contribution of diffusion. Table R2 shows that local search and simulated annealing match or exceed D3AO’s reported mean performance using the same fitted revenue model and evaluation budget. Table R3 shows no improvement from the learned prior in any reported seed-level comparison. What demonstrated benefit does the diffusion component provide over directly optimizing the learned revenue model? Even though you revise the claim to be comparable, that nevertheless makes your work itself less attractive in the contribution, especially the "near-optimality" contribution is claimed empirically.

  2. Manuscript revisions. The latest PDF available to me appears unchanged: Is there a way to update your revised manuscript as mentioned in your comments? I understand if the system does not allow it, and if that's the case, please elaborate more on what you add for the additional uncited literature review and the claim towards the "pessimistic estimates", use of the Boltzmann assumption, and the revised limitations?

  • You distinguish your work against Guo et al. (2025), Li et al. (2025), NAO by "learns a generative prior from offline data and guides sampling with an estimated choice model", but this does not, by itself, make those general assortment optimizers inapplicable. I feel that, to make the paper complete, the comparison with such benchmarks, for example NAO, is still needed since they are direct comparators, but I understand it might not be possible due to time constraints. So at least you need to make the comparison clearer and explain more convincingly the distinctions and why you are not comparing these methods.
  • Talking back to my first point: what you have compared, the ordinary local search methods, already leaves the diffusion-specific benefit unestablished, so you may need to address this first. If the optimality ratio won't be distinguishable, what are some other possible performance metrics to make the contribution clear? Under the same setting, but fewer evaluations, lower total computation, more useful diversity, or robustness in a setting where existing local search methods fail?
  1. Consistency of experimental results. For non-Boltzmann logging under MMNL with N=80N=80, Table 9 reports oracle maxima of 91.34% and 80.36%, whereas Table R1 reports 98.73%. I understand that the new experiments use regenerated data. Please clarify the differences between these experiments and whether the new results supersede Table 9.
Reviewer_yEcxOpenReview ↗
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Paper summary

The paper studies offline assortment optimization using logged assortment–choice data. It proposes D3AO, which learns a neural choice model and a discrete diffusion prior over assortments, then guides reverse diffusion with coordinate-wise estimates of revenue gains. Experiments on synthetic MNL, MCCM, and MMNL settings compare D3AO with parametric estimate-then-optimize baselines.

Critical strengths
  1. A coherent, optimization-oriented diffusion framework. Section 4 clearly distinguishes the learned generative prior from the reward-guidance mechanism. Theorem 2 shows that the logit update exactly solves a KL-regularized local-improvement problem for the specified coordinate-wise surrogate, giving the guidance rule a firmer foundation than an ad hoc sampling heuristic.

  2. Controlled experiments highlight the impact of guidance. In Figure 2, unguided diffusion performs consistently worse than guided variants across MNL, MCCM, and MMNL data, while the guided methods achieve high reported optimal-ratio statistics. This ablation supports the more focused claim that reward guidance, rather than diffusion sampling alone, drives the reported performance.

Critical weaknesses
  1. The headline solution-quality comparison relies on oracle ground-truth revenue to evaluate generated candidates, so it does not establish the quality of an assortment D3AO can return offline. In Section 5, each diffusion method generates 256 candidates, and the paper reports their maximum, mean, median, and 90th-percentile true optimal ratios, evaluating R(s)R(s) under the ground-truth choice model. Each parametric baseline, by contrast, returns one assortment. The maximum over 256 samples is useful as a measure of candidate-set coverage, but it is not a fair comparison of decision quality unless the paper specifies a practical candidate-selection rule. At deployment, the true RR is unavailable, so selecting arg⁡max⁡mR(s(m))\arg\max_m R(s^{(m)}) is impossible. Selecting by R^θ(s(m))\hat R_\theta(s^{(m)}) could yield different results, especially under the model misspecification and distribution shifts emphasized by the paper. This concern is compounded by the abstract’s reference to “pessimistic estimates”: Section 3, Step 2 uses the ordinary plug-in estimate R^θ(s)\hat R_\theta(s), and Section 4.2 uses it directly in the guidance term, without an uncertainty estimate, lower confidence bound, or other conservative adjustment. The authors should report the true revenue of the single candidate selected by an available offline rule—for example, arg⁡max⁡mR^θ(s(m))\arg\max_m \hat R_\theta(s^{(m)}) or a held-out conservative estimator—and compare that returned decision with the baselines under the same protocol.

  2. The experiments do not establish whether diffusion improves on direct optimization of the learned reward model, and they omit a relevant neural assortment-optimization baseline. Since D3AO learns a flexible neural choice model and uses it to define a differentiable or queryable plug-in objective, the empirical contribution depends on showing that diffusion-based search outperforms methods designed to optimize the same learned reward. Section 5 compares D3AO only with MNL-MLE and MCCM-EM, which are deliberately misspecified in the MMNL setting. This demonstrates robustness relative to those specific parametric baselines, but does not support the broader claim that guided diffusion is an effective model-agnostic optimization framework. A comparison with Neural Assortment Optimization—or, at minimum, strong direct-search baselines optimizing the same reward under comparable compute and candidate budgets—is needed to establish the diffusion procedure’s added value.

Questions for authors

In Section 5, what rule selects a single deployable assortment from the 256 guided samples? Please report its true optimal ratio when selection uses only information available offline, such as the learned plug-in revenue estimate or a held-out conservative estimate. If the reported gains persist for the selected assortment, that would substantially address my main concern.

1 comment

We thank the reviewer for the precise and constructive review. Both of your main concerns are correct, and we address them with new experiments and revisions.

Setup for all new results. Regenerated data (Boltzmann policy, β0=1\beta_0=1, n=10,000n=10{,}000 unless stated), paper hyperparameters (T=100T=100, λmax⁡=1000\lambda_{\max}=1000, γ=3\gamma=3, 256 samples), 10 seeds. Entries: true optimal ratio (%), mean ± std. Optima are exact (MMNL: Gurobi MILP, zero gap, all certified). Ground truth is used only for evaluation. "Shifted" = non-Boltzmann logging: uniform size, then a uniform random subset.

W1. Oracle maximum, deployable selection, "pessimistic"

(a) We relabel the reported maximum as "oracle best-of-256", a measure of candidate coverage only. The reported mean is the expected ratio of one assortment drawn from the sampler, a rule that needs no oracle.

(b) Selection rule. D3AO now returns s^=arg⁡max⁡s∈CR^θ(s)\widehat s=\arg\max_{s\in\mathcal C}\widehat R_\theta(s) over the distinct candidates C\mathcal C, using the same revenue estimate as for guidance; no ground truth or new interactions.

(c) Results (Table R1, N=80N=80). The two baselines are rerun on the same instances; each returns one assortment.

MethodMNLMCCMMMNLMMNL shifted
D3AO oracle best-of-25699.88±0.1199.85±0.2197.93±0.8798.73±0.77
D3AO returned99.84±0.1599.77±0.2097.13±1.0097.20±0.94
MNL-MLE99.99±0.0199.63±0.4148.49±7.2796.49±2.68
MCCM-EM99.50±0.5399.57±0.4552.46±10.7997.89±1.00

The returned assortment is within 0.1 points of the oracle on MNL/MCCM and about 1.5 points on MMNL. Correctly specified baselines are near-optimal and D3AO is within 0.2 points of them. Under MMNL with Boltzmann data, both misspecified baselines return 1–2 products (~50%), versus 97.13% for D3AO. Under shifted logging, which covers the space evenly, both recover and MCCM-EM is slightly better than D3AO (higher on 8/10 seeds). D3AO's advantage is thus large when logged assortments are concentrated, not under uniform exploration.

(d) "Pessimistic" was inaccurate: D3AO uses a plug-in estimate. We revise the abstract to "model-based estimates of expected revenue" and list uncertainty-aware selection as future work (not evaluated here).

W2. Direct optimization of the same learned reward

Using the same fitted R^θ\widehat R_\theta and the same number of R^θ\widehat R_\theta evaluations (2N2N per sample per step), we compare multi-start local search (add/drop), simulated annealing (SA) and random search; all return one assortment by rule (b).

Table R2.

MethodMNL 40MNL 80MNL 120MMNL 40MMNL 80MMNL 120
D3AO99.7499.8499.3894.2597.1397.29
Local search = SA99.7499.8499.8594.2597.6097.78
Random91.7476.1574.9685.3074.9369.02

(Means over 10 seeds, std 0.2–7.5; LS and SA coincide.) On MMNL N=80N=80, LS/SA reach 97.60 already at 1/16 of the budget (D3AO: 97.28 at that budget).

Table R3. Learned prior vs. none (gϕ=0g_\phi=0, same guidance; MMNL, returned assortment, means).

SettingD3AONo priorseeds worse/tied/better
NN=80, nn=1,00097.4197.410/10/0
NN=80, nn=3,00097.4597.481/9/0
NN=80, nn=10,00097.1397.605/5/0
NN=80, shifted97.2097.482/8/0
NN=4094.2594.250/10/0
NN=12097.2997.788/2/0

The results do not support an advantage of diffusion search over direct optimization, and the learned prior does not help in any setting. Local search almost always reaches the same maximizer of R^θ\widehat R_\theta, so quality is limited by reward estimation, not by the optimizer; random search is far worse, so the problem is not trivial.

Revised claims. We remove the claims that diffusion search beats direct optimization and that the prior improves quality. We state that D3AO is comparable to strong direct search on the same reward (slightly worse at larger NN), that the main error source is reward estimation, and, as a limitation, that these benchmarks cannot show a benefit of the prior. We did not compare with NAO, genetic or continuous-relaxation methods in this period.

Q1

See W1(b) and Table R1: the returned assortment uses offline information only.

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