acceptodds
Under review as a conference paper at ICLR 2027

The Problem Is the Problem: Towards Scalable Mathematical Discovery

Abstract

AI systems are increasingly capable of contributing to mathematical research. In research practice, frontier-model reasoning is a limited resource, and expert mathematical review is even more sharply constrained. Allocating these scarce resources well is therefore central to making AI-assisted mathematical discovery efficient. In most current AI-for-math workflows, human effort is concentrated at the beginning and end, in selecting suitable research problems and later reviewing the resulting artifacts. These two stages are becoming bottlenecks for research-level mathematics. We address them by proposing a new human-AI discovery paradigm. The human input is no longer a single problem selected in advance, but a research direction in which the experts have interest and expertise. The system then searches a broad literature corpus for candidate problems in that direction. Inspired by search and recommender systems, we build Find, Attempt, and Recommend (FAR), a literature-to-review cascade that automates the search for suitable problems and focuses human attention on artifacts that have passed several stages of filtering. In a combinatorics pilot, the pipeline starts from 5,245 combinatorics papers, recovers 6,453 candidate conjectures or open problems, and filters them to 4,717 apparently well-posed and still-open conjectures. Subsequent reasoning and automated triage stages surface 598 potential resolutions and select 77 items for author-team review. Among them, human experts identify many interesting discoveries, including results on conjectures and questions of Davies-Jenssen-Perkins-Roberts, Erdős-Straus, Ikenmeyer-Pak-Panova, and Lund-Saraf-Wolf. These results demonstrate the effectiveness of this new mode of human-AI collaboration for mathematical discovery.

Primary area:
foundation or frontier models, including LLMs
Keywords:
AI for Mathematics, Large Language Models, Scientific Discovery

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_SRCCOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes FAR (Find, Attempt, Recommend), a cascade that takes a research direction where i) an LLM labels papers in a corpus, extracts unresolved statements, checks with web search whether they are still open, ii) a stronger model attempts each one once, three samples of the same model judge the claimed resolutions, and iii) a grader sorts the survivors by novelty and significance for human review. A combinatorics pilot (51,110 papers, gpt-oss-120b, Gemini 3.5 Flash, Gemini 3.1 Pro, GPT-5.5 at xhigh) yields 4,717 "open" conjectures, 1,050 claimed resolutions, 598 judged correct and 77 graded publishable. The authors hand-check 15 chosen by interest. A second part frames which conjectures to attempt as budgeted selection, validates LLM difficulty and importance scores against the run's outcomes, and compares ranking strategies by 5-fold cross validation. Appendix C writes up the 15 results.

Critical strengths
  1. The pipeline produced real mathematics. I checked the arguments in C.2, C.5, C.8, C.10, C.13 and C.14 in detail and spot-checked C.3 (the m = 1 values 81 and 200 are right), C.9 and C.15. I found no errors. I also confirmed that Conjecture 2 of Davies et al. (2018), Conjecture 1.4 of Lund et al. (2018) and Conjecture 5.2 of Ikenmeyer et al. (2024) are stated exactly as the paper quotes them, so the three flagship results address what they claim to address. Section 4.4 is candid that one reviewed result was already known, one is a classical construction, and C.13 was published independently by two groups.
  2. The funnel is reported stage by stage, the prompts are given in full, and the paper documents its own literature-check failure (Erdős #635). The writing is clear.
Critical weaknesses

1. The cascade lacks a representative audit and a matched comparison with existing problem pools.

Only 15 of the 77 recommended artifacts were reviewed, "chosen by our own interest" (Section 4.4), so 15/15 is not an estimate of precision for the 77, let alone for the 598 that passed judging. No reviews from the 452 FAIL or 2,905 NONE outcomes were reported, so the false-negative rate is unknown.

The pool is also softer than the headline number. The attempt stage reclassified 443 + 319 = 762 of the 4,717 "apparently well-posed and still-open" conjectures (16%) as known or defective, grading removed 75 more as known, and Figure 3's caption mentions a "later status recheck" that reclassified further candidates without saying how many.

The model that wrote the proofs also judges and grades them, and the "three independent judges" (Section 4.1) are three runs of that model. The paper gives no agreement statistics and uses no second model family.

Finally, for a paper whose premise is that frontier reasoning is a scarce resource, no token, dollar or wall-clock cost is reported for any stage, and there is no comparison with the obvious alternative of pointing the same solver at an existing pool. Feng et al. (2026), which the paper cites, already swept 700 Erdős problems with a review stage. Formal Conjectures (Firsching et al., 2026) formalizes 1,029 open conjectures in Lean, and pipeline-math (Peng et al., 2026) attempts published open-problem lists. The paper cites all three but does not say what literature mining buys over them in yield per attempt or per dollar. The appendix shows the cascade can produce correct new mathematics. How often it does so, at what cost, and whether mining beats an existing pool are not measured, and without those the abstract's "demonstrate the effectiveness" is not well supported.

2. The allocation analysis is thin as it relies on automated outcome labels and retrospective strategy selection.

The bandit framing is decorative. Each arm is pulled once (Section 2), so the problem is supervised ranking, and Appendix B.1 is linearity of expectation plus the textbook (1−1/e) greedy bound.

Score validation is LLM against LLM, with Gemini 3.1 Pro's scores tested against outcomes GPT-5.5 produced. The association is real but overstated. Section 4.3.1 reports AUC 0.69 for difficulty and 0.60 for importance and calls both "strong positive correlation" on the strength of Mann-Whitney p-values. A small p-value only shows that an association exists, and at these sample sizes a weak one is enough to produce it. The AUC is the size of the effect. By the paper's own definition, 0.60 means the importance score ranks a random publishable resolution above a random non-publishable one 60% of the time, against 50% for a coin flip. The stratified AUC of 0.56, also in Section 4.3.1, is said to show that difficulty "still effectively separates" solved from unsolved attempts within an importance stratum. It shows a modest conditional effect, since about two thirds of the excess over 0.5 disappears once importance is held fixed. The scores carry signal, as the gains below show, but not a strong one.

The f3f_3 recommendation, "discard all but the most important part of P and rank what remains", was chosen after seeing the outcomes ("of the fractions we tried, keeping the most important 1/10 did best on this run"). Tables 1 to 3 suggest how little it rests on. Inside the top decile the strategy plateaus at 2.00 expected artifacts, 1.70 expected total importance and 0.850 expected max importance from B = 200 onward, which reads most naturally as two artifacts of importance about 0.85. If so, the f3f_3 conclusion depends only on two conjectures.

On f2f_2, the paper notes that ranking on p^\hat p beats the prescribed i⋅p^i \cdot \hat p at every budget and leaves it there. Since i⋅pi \cdot p is optimal for f2f_2 under the true pp, the reversal most likely comes from error in p^\hat p or from noise in a single run's outcomes. The simplest explanation could be that p^\hat p overestimates success on important conjectures. They are rarely solved (the top decile by importance yields 2.00 artifacts at B = 300 where uniform random yields 5.17, Table 1), and the p^\hat p ranking avoids them (the max importance among the artifacts it returns averages 0.50 at B = 300, against 0.85 for the top-decile strategy, Table 3), so weighting by ii pushes the selection back toward conjectures that fail. A plot of p^\hat p against realized outcomes by importance bin would show whether this is right. "Narrowly" also undersells the gap at small budgets. At B = 10, Table 2 gives 0.09 for i⋅p^i \cdot \hat p against 0.16 for p^\hat p and 0.08 for uniform random, so importance weighting gives up most of the gain over random.

What the section does establish is that ranking on p^\hat p raises the expected artifact count from 5.17 to 7.92 at B = 300 (Table 1) and the expected total importance from 2.51 to 3.87 (Table 2), about 1.5x uniform random in both cases. However, this is a result on one run, with outcome labels that GPT-5.5 produced and strategies compared after the fact, and the paper itself notes that it depends on the scoring model, the pool and the cascade (Section 4.3.2). Whether it transfers to another pool or solver is untested.

Lastly, the paper does not discuss directly relevant work on predicting difficulty to allocate inference compute. For example,

Snell, Lee, Xu, Kumar (2024). Scaling LLM test-time compute optimally can be more effective than scaling model parameters. arXiv:2408.03314.

Damani, Shenfeld, Peng, Bobu, Andreas (2024). Learning how hard to think: input-adaptive allocation of LM computation. arXiv:2410.04707.

Questions for authors
  1. Could you verify a uniformly random sample of the 598 PASS outcomes and of the 77 artifacts for correctness and novelty, and report the novelty status of all 77? How many of the 77 are already in the literature?

  2. Could you report cost per stage (tokens or dollars, and wall-clock) and cost per correct new artifact? Would it be possible to run the same attempt, judge and grade stack on an existing pool of comparable size, e.g. Erdős problems, Formal Conjectures, Open Problem Garden, and compare yield per attempt and per dollar with the mined pool?

  3. Could you give the distribution of judge votes over the 1,050 claims (3/3, 2/3, ...) and the PASS rate when one judge is replaced by a different model family? How often do the three GPT-5.5 judges disagree?

3 comments

We thank the reviewer for the very careful reading. We respond to the weaknesses and questions below.

W1. Audit, pool quality, judging, and cost.

  • Audit of the 77. We agree that the 15 reviewed artifacts are not enough to estimate the precision of the 77. The 15 show that the workflow can surface correct and interesting mathematics, which was far from routine with the models available in April–May 2026, when most of this work was done. A full check of all 77 artifacts is beyond our expertise and the scope of this paper, and it is not how FAR is meant to be used: each mathematician reviews only the results that match their own interests and expertise. We did not check the FAIL or NONE outcomes either. We will fully open-source the code and pipeline, together with all intermediate data (including the FAIL and NONE outcomes, the judge verdicts, and the grader's novelty reports), so that interested mathematicians can read, check, and use them. We do not claim credit for any of the mathematical results.
  • Pool size and quality. For this demonstrative run, we used 51,110 mathematics papers randomly collected from OpenAlex, without curation, so the pool is an unbiased sample of open problems as they are actually stated in the literature. It therefore naturally contains statements that have since been resolved or are defective as written, and we report every such reclassification in the outcome tree (Section 4.2). The cascade is designed for this: early stages are deliberately permissive, and later, stronger stages check the literature again (Section 3.2).
  • Same model for attempting and judging. We agree that this may increase false positives. Like a recommender system, the cascade tolerates some errors because a mathematician sits at its end and makes the final check. Each stage is also fully customizable. In this pilot the solver is a single gpt-5.5 attempt (pass@1), for demonstration only, and users can replace it, or the judges, with stronger agent systems of their own.
  • Cost and comparison with existing pools. We think these pools are not directly comparable with FAR. Feng et al., Formal Conjectures, and pipeline-math are built around curated lists of well-known problems. FAR starts from a research direction chosen by a mathematician and asks which open problems in that direction, many of them on no list, are worth their attention. Yield per attempt or per dollar on a curated list therefore answers a different question. For our own question, the paper does include an ablation: Section 4.3 compares allocation strategies against the uniform allocation used in the pilot, with the budget measured in attempts.

W2. Allocation analysis.

  • Bandit framing. We agree that a bandit view supports multi-round allocation, which would be more efficient in principle. It also needs many more attempts and much more compute. Given our resource constraints, we first analyzed the single-round case, which corresponds to the initialization step of a bandit algorithm (Section 2.3), and leave the multi-round case to future work.
  • Strength of the scores and the empirical results. We agree with the reviewer and will revise our wording. The scores still carry a meaningful signal. At small budgets only a handful of artifacts are selected, so the results are noisy. Together with error in p^\hat{p} on important conjectures, as the reviewer suggests, this likely explains the p^\hat{p} vs. ip^i\hat{p} reversal and the gap at B=10B=10. We used 5-fold cross-validation averaged over 1,000 random partitions to reduce this noise, but the results still depend on a single run over about 4,700 conjectures. We hope to scale up in future work to reach more definitive conclusions, and we will add this to the limitations.
  • Related work. We thank the reviewer for pointing out Snell et al. (2024) and Damani et al. (2024), which are relevant. We will add citations.

Q1. Random-sample audit. We did not run one, for the reasons in W1. All 77 artifacts will be released with the grader's novelty reports.

Q2. Cost and comparison with an existing pool. See W1. Each conjecture received one gpt-5.5 xhigh agent run, which is the unit of budget in our demonstrative run and our analysis.

Q3. Judge votes. We did not use a second model family, for the reasons in W1. All judge verdicts on the 1,050 claims will be released. The mathematician makes the final check, and every stage is customizable. When we ran the pilot in April–May 2026, in our experience no other model available to us came close to gpt-5.5 on research-level mathematics, so we used it throughout and kept each stage minimal for demonstration. Users can add judges from other model families.

We thank the reviewer again for the constructive comments. We hope these answers address the reviewer's concerns, and that the reviewer will reconsider the evaluation.

Thank you again for your time and feedback. We would like to kindly check whether our responses have addressed your concerns. If anything remains unclear, we would be happy to clarify further, and we would be grateful if you would consider updating your score.

Thanks for the reply, and for agreeing to tone down the wording on the scores and add Snell et al. and Damani et al.

I'm keeping my score, because the 15 results only show FAR can discover real math but not how often its picks are correct and new.

Releasing everything later is great, but some of it you could report now, like the judge vote split over the 1,050 claims and whatever per-stage cost numbers you logged. One attempt per conjecture doesn't tell us what the pipeline cost. Also, how many of the 77 artifacts fall in the top tenth by importance? That would show how many conjectures the f3f_3 result rests on.

I get that checking all 77 is out of scope. My ask for a correctness check was a random sample. At minimum, the abstract should say 77 items were recommended and you checked 15, chosen by interest.

Reviewer_7JipOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces Find, Attempt, and Recommend (FAR), a pipeline that extracts open problems from mathematical literature, attempts solutions, and recommends promising results for expert review. In a combinatorics study, it attempts 4,717 candidate problems and selects 77 artifacts for review. The authors examine 15 selected artifacts and report that all are mathematically correct, although one result was already known. The paper also studies strategies for allocating attempts using model-generated difficulty and importance scores. Its main contribution is a demonstrated discovery workflow supported by concrete proofs and counterexamples.

Critical strengths

The strongest contribution is the mathematical results obtained through the pipeline. The paper provides detailed proofs and counterexamples addressing published conjectures and questions. The reviewed examples provide concrete evidence that searching a broad literature corpus and filtering proposed solutions can lead to useful mathematical discoveries. These outcomes are the main reason for my positive assessment, even though the individual pipeline components are relatively straightforward.

Critical weaknesses
  1. Mathematical importance is assessed mainly by models. The importance scores guide problem selection and are also used to evaluate the allocation strategies, but their agreement with expert judgment is not established. Human involvement is concentrated on reviewing selected outputs. I would have liked an evaluation involving mathematicians earlier in the process—for example, assessing candidate priorities or providing feedback on the shortlist—to test whether the system directs effort toward problems they consider worth pursuing.

  2. The human evaluation does not establish the reliability of the overall recommendation process. The authors examine 15 of the 77 recommended artifacts, selected according to their interests. This supports the reported examples, but leaves uncertainty about the correctness, novelty, and significance of the remaining recommendations.

Questions for authors
  1. Have domain experts independently ranked a sample of candidate problems by importance? How closely do their rankings agree with the model scores, and would expert rankings change which problems receive effort?

  2. Beyond being selected according to the authors’ interests, what determined which 15 artifacts received human review? Were any other recommended or rejected artifacts checked, and what were the outcomes?

2 comments

We thank the reviewer for recognizing the mathematical results as the main contribution. We respond to the weaknesses and questions below.

W1. Importance is assessed by models. We agree that model-generated importance scores are not fully reliable, and we thank the reviewer for this point. We note, however, that mathematicians are involved early in the pipeline. They choose the research direction, at any granularity they need, and they can choose the corpus, e.g., the back issues of a few leading journals in their field. Both steps already shape which problems enter the pool. In our pilot we deliberately put little effort into these steps, and simply used 51,110 mathematics papers randomly collected from OpenAlex, so that we could see what the pipeline produces without our own selection bias. In the released tool, mathematicians will also be able to adjust and re-rank the candidate problems themselves.

W2. Reliability of the overall recommendation process. We agree that the 15 reviewed artifacts are not enough to estimate the precision of the 77. The 15 show that the workflow can surface correct and interesting mathematics, which was far from routine with the models available in April–May 2026, when most of this work was done. A full check of all 77 artifacts is beyond our expertise and the scope of this paper, and it is not how FAR is meant to be used: each mathematician reviews only the results that match their own interests and expertise. We will fully open-source the code and pipeline, together with all intermediate data and all 77 artifacts, so that interested mathematicians can read, check, and use them. We do not claim credit for any of the mathematical results.

Q1. Expert ranking vs. model scores. We ranked the 15 reviewed artifacts by importance within the author team. Although it is hard for us to agree on a strict total order, our ranking correlates strongly and positively with the model's importance scores.

Q2. How were the 15 artifacts chosen, and were others checked? The 15 were chosen by the authors' own interests, which matches how FAR is designed to be used. We did not check the rejected artifacts. As noted above, all intermediate outputs, including the rejected ones, will be released so that anyone can check them, and we do not claim credit for any of the results.

We thank the reviewer again for the constructive comments. We hope these answers address the reviewer's concerns, and that the reviewer will consider raising the score in support of our work exploring a new way of using AI in mathematical research.

Thank you again for your time and feedback. We would like to kindly check whether our responses have addressed your concerns. If anything remains unclear, we would be happy to clarify further, and we would be grateful if you would consider updating your score.

Reviewer_ckyJOpenReview ↗
Rating
2(+1)
Confidence
2(−1)
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper proposes a method to select mathematical problems for mathematicians. The way they approach this is to extract a pool of conjectures from a subarea (combinatorics), then attempt these conjectures using LLMs, and recommend them for further study by human experts.

Critical strengths
  1. They actually checked a small number of proofs (15 of them), and some of them were (after a cursory glance) still open, so perhaps have significance. These include a proof of the Ikenmeyer–Pak–Panova conjecture and a counterexample to the Davies–Jenssen–Perkins–Roberts conjecture.
  2. They were aware of and reported their own failures. The paper itself flags the Erdős #635 result as already known and the Lund–Saraf–Wolf construction.
Critical weaknesses

The critical weakness is the quality of the execution. The pipeline didn't appear to work very well and there were no ablations. In particular, using these (mostly closed) LLMs with no ablation on the labelling, extraction, and checking, is a major weakness.

Also, I'm not docking points for this, since it is more of a normative and philosophical view that I'm unsure is widely shared at this point, but I don’t think this approach makes sense. Read Thurston on the point of mathematics: https://arxiv.org/pdf/math/9404236. Problem selection is tangled up with the interests and skills of the human. Significance is in the eye of the beholder.

If the method had been described clearly, was novel and significant, and the evaluations were more thorough, then I would have been open to giving a higher score. As things stand, this was not close.

Questions for authors

Figure 2 is very poorly put together - text clipping, hard to read, etc. “The upper row shows a search or recommender pipeline that recalls and filters candidates from a large corpus.” Can you pick or communicate clearly?

I used an LLM and it agreed with the novelty issue with the Erdos problem the system solved, and found more issues beyond it. Would you care to comment?

LLM: The novelty checks leak. Of the 15 artifacts the authors reviewed, two rest on prior work that the cascade did not catch. The Erdős divisor-difference result (Erdős problem #635) was already resolved on the Erdős problems site before the run, and Tao notes there that it follows from an inequality of Elliott from 1979. The Lund–Saraf–Wolf counterexample is the Bruen–Drudge (1999) construction, also studied by Cossidente–Pavese (2017); the paper acknowledges this and frames the contribution as the connection to the conjecture. Upstream, the "still open" check let through 443 conjectures that the attempt stage then found already resolved, and grading caught 75 more. Because the 15 were chosen by interest rather than at random, the paper gives no estimate of how many of the 77 "publishable" artifacts are actually new. I would like to see a random sample (added by the human reviewer: or all of...) of the 77 checked by someone outside the author team, and the rate at which each stage misses prior work.

4 comments

We thank the reviewer for the careful reading. For context, most of this work was done in April–May 2026, and we hope the reviewer will take this into account.

W1. Execution quality. In April–May 2026, AI resolving even an ordinary research-level open problem was still rare (e.g., arXiv:2603.29961 and arXiv:2604.06609 by internal OpenAI models). Our author team includes professional mathematicians who wanted to use AI on many many problems at once rather than one at a time. Starting only from combinatorics, the pipeline produced a proof of the Ikenmeyer–Pak–Panova conjecture, counterexamples to the Davies–Jenssen–Perkins–Roberts and Lund–Saraf–Wolf conjectures, an answer to an Erdős–Straus question, and other results we reviewed and found correct. We think these are of interest to the community and worth sharing. Given model capabilities at the time, we expected far fewer interesting results and many plausible-looking but wrong proofs. We did not find the latter: all 15 artifacts we reviewed are mathematically correct. If there are specific aspects of the execution the reviewer found lacking, we would be glad to address them.

W2. No per-stage ablations. We agree that per-stage ablations would be informative. But our goal is not to benchmark LLMs on labeling, extraction, or checking. It is to propose a new workflow, in which a mathematician gives a research direction instead of a single problem, and to study how to allocate compute over the resulting pool. We are not aware of an earlier system that does this. For this goal, the paper does include an ablation of the allocation step (Section 4.3).

W3. Thurston and problem selection. We agree with this view, and FAR is built on it: problem selection depends on the interests and skills of the mathematician. A major purpose of FAR is to help mathematicians find problems that interest them and on which progress is still being sought. Many mathematicians, especially junior researchers, are broadly interested in an area, but finding specific problems usually depends on conversations with colleagues, occasional workshops, their own reading, or guidance from senior researchers. Many good problems never reach the people they would interest, and AI can lower this information barrier. The difficulty and importance scores are only a coarse filter, e.g., to drop trivial cases. The mathematician sits at both ends of the pipeline because both the choice of direction and the choice among the recommended candidates depend on their own taste and expertise. We hope the evaluation can take into account both the novelty of this workflow and what it achieved with the models available in April–May 2026.

Summary of weaknesses. The method is described in detail in Section 3, with all prompts in Appendix A. We will fully open-source the code and the complete pipeline, together with all intermediate data produced during the run, and we do not claim credit for any of the mathematical results. How significant this system is depends on the reviewer's taste, but we hope that, given the context above, the reviewer will reconsider the evaluation.

Q1. Figure 2. We could not find any clipped text in Figure 2. We would be grateful if the reviewer could point out where. The upper row shows a standard cascaded recommender system, as widely used in industry (e.g., TikTok and YouTube). See the references in Section 3 [Wang et al., 2011; Chen et al., 2017; Liu et al., 2022] for more details. We include it to show the analogy with FAR. We will improve the wording in the revision to make this clearer.

Q2. Novelty issues raised by the LLM. Thank you for raising these. Both cases are discussed in the paper.

  • Erdős 635: Section 5.1 states that this result was already on the Erdős problems site. The model found a proof independently, but the novelty check missed the prior record. As expected with the agents available at the time, novelty checks are imperfect. The cascade only aims to surface results that are likely to be new, and users are expected to check prior work themselves.
  • Lund–Saraf–Wolf: Section 5.2 states that the construction already exists in the literature in a different context. What is new is that it refutes this particular conjecture. As of late 2025, Tao's survey (arXiv:2511.07721) still lists the conjecture as open, so the community had not noticed this connection.

Q3. Checking all 77 artifacts. A full check of all 77 artifacts is beyond our expertise and the scope of this paper, and it is not how FAR is meant to be used: each mathematician reviews only the results that match their own interests and expertise. The 15 artifacts we reviewed show that the workflow can surface correct and interesting results. All outputs will be released for interested mathematicians to read and use.

We hope the added context and answers address the reviewer's concerns, and that the reviewer will reconsider the evaluation.

Thank you again for your time and feedback. We would like to kindly check whether our responses have addressed your concerns. If anything remains unclear, we would be happy to clarify further, and we would be grateful if you would consider updating your score.

As the discussion period is ending soon, we would like to kindly check whether our responses have addressed your concerns. We would be happy to clarify anything further, and we would be grateful if you would consider updating your score.

I'm sympathetic to the author's arguments about the paper submission timeline, and the extremely fast pace of advancement in mathematical theorem proving.

I am not competent to assess the quality of the generated proofs for these statements since it is outside my area of expertise.

To review this work as it stands requires both a specific expertise in theoretical mathematics as well as a machine learning archicture expertise.

Therefore, I am increasing my score from 1 to 2 and reducing my confidence from 3 to 2.

-- A couple small notes:

  1. If the authors plan to re-submit this work at a subsequent ML-focused conference, I might recommend including human studies. This would alleviate the issue of finding reviewers who are both capable of direct evaluation of these proofs as well as the ML method that produced them.
  2. Figure 2: "Item corpus" touches the top of the cylinder, and the top ("Search and recommender system cascade") and bottom ("Find, Attempt, and Recommend cascade") text are too close to to the pipeline diagram. I also think that the caption could be expanded to provide clarity to the figure's stages.

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

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