acceptodds
Under review as a conference paper at ICLR 2027

ArchitectureIQ: On the Measure of Model Intuition

Abstract

Top researchers have good intuition, but do language models have as good intuition about model training as top AI researchers? To measure model intuition of LLMs and humans, we introduce the **ArchitectureIQ** benchmark. Each question presents a synthetic dataset and several training recipes, and the test-taker is asked to predict the recipe yielding the best test metric. Overall, we find that LLMs' model intuition is good but has four limitations: **(1) The intuition is imperfect, or even sub-human in some cases.** Frontier models achieve around 76% accuracy (random choice 33%) vs best human researcher (66.0%), yet remain far from perfect. For architecture-only questions, best human achieves 65% while GPT-6 Astra only has 38%. **(2) The intuition is empirical, not structured**, supported by the fact that more CoT compute does not lead to substantial improvement. Unlike math, we still lack a "Science of AI" language that enables structured reasoning on AI. **(3) The intuition is not maximally condensed**, and can be further compressed into a knoledge base. Our constructed knowledge base with only 20 items yields large gains for weak models: GPT-4o equipped with the accumulated knowledge almost matches the performance of Claude Opus 5. **(4) The intuition is insensitive to dataset properties**, but the best model should in general depend on data properties. This suggests that data is the real "dark matter" in AI - LLMs (so do human researchers) understand too little about data, even less than model architectures.

Primary area:
datasets and benchmarks
Keywords:
large language models, neural network training, training outcome prediction, automated AI research, experimental intuition

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_UbU2OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces ArchitectureIQ, a benchmark of 500 three-choice questions. Each question shows a synthetic dataset (regression, tabular/XOR/spiral classification, or bigram LM) and three training recipes (model plus optimizer settings, sharing the same data, loss, batch size, and step budget). The test-taker predicts which recipe reaches the lowest final test loss. Ground truth comes from running each recipe for 10 seeds, and a question is kept only if the winner's worst seed beats every rival's best seed.

Frontier LLMs reach about 76% accuracy (85–87% on optimizer-only questions, 38–61% on architecture-only). Ten human ML researchers average 51% on a 50-question subset, and the best scores 66%. The paper then argues that LLM "model intuition":

  • is unstructured, because few-shot examples and more reasoning effort don't help;
  • is compressible, because a 20-proposition knowledge base distilled from Claude Opus 5 lifts GPT-4o from 53% to 68% on a 50-question subset;
  • is insensitive to data, because on 52 paired questions where only the dataset changes and the winner flips, accuracy drops to 46–50%.
Critical strengths
  1. The execution-grounded design is solid. Every label comes from actually running the generated code over 10 seeds with a strict separation filter, choice order is randomized, and the release audit checks prompt–program agreement and leakage (Appendix A.3–A.4).
  2. Using synthetic datasets to avoid contamination from known benchmarks is a sensible choice. The generator allows controlled variants, such as varying the number of choices (Fig. 3) and paired dataset swaps (Sec. 3.2, Appendix E).
  3. The paired label-flip evaluation is the most interesting result. Models switch their answer on only 6–23% of pairs when only the dataset changes and the correct answer flips. This is a clean, informative test of whether predictions use the data at all.
  4. The paper compares against non-LLM baselines (heuristics, logistic regression, a depth-4 tree, and an analytical decision policy), which helps interpret what the LLM numbers mean.
Critical weaknesses
  1. The benchmark mostly measures short-horizon optimization speed, not "model intuition" in the sense claimed.

    • All models are tiny: MLPs of width ≤256 and depth ≤5, or 1–4 layer Transformers/GRUs.
    • Datasets have 256–2,048 points, and training runs only 256–2,048 steps (Appendix A.2).
    • In this regime, the winner is largely determined by how far parameters move in the given steps. The paper's own evidence confirms this:
      • an analytical policy based on an integrated effective-learning-rate proxy reaches 78.2%, above every LLM (Appendix C.3);
      • logistic regression on configuration features reaches 74.2%;
      • most knowledge-base entries are budget-specific rules such as "Within T ≲ 256 steps, rank candidates by stable effective step size" (Fig. 6).

    This explains why optimizer-only questions are easy (85–87%) and architecture-only questions are near chance. Architectural knowledge from real-world practice (depth, residuals, LayerNorm help) often doesn't apply to 256-step training of tiny MLPs. Table 4 supports this reading: on architecture-only questions, GPT-4o (52%) and Llama 3.1 70B (49%) outperform most frontier models (38–48%). That suggests frontier models apply real-world priors that are wrong in this regime, not that they lack intuition. The title and abstract ("do language models have as good intuition about model training as top AI researchers?") claim far more than this regime supports.

  2. The "first benchmark" claim is incorrect, and closely related work is missing. "Predicting Empirical AI Research Outcomes with Language Models" (Wen et al., NeurIPS 2025) already benchmarks LLMs and 25 human experts on predicting which of two research ideas performs better on real benchmarks, with execution-grounded labels from papers. LLM-assisted hyperparameter optimization (e.g., LLAMBO, ICLR 2024, and LLM-as-HPO work) also directly studies whether LLMs can rank training configurations before running them. These need to be discussed. The contribution should be repositioned as a controlled, synthetic, executable variant of this problem.

  3. The human comparison is too small to support the stated conclusions.

    • Humans answered a different 50-question subset (22 architecture, 16 optimizer, 12 mixed), while models are scored on all 500.
    • The headline compares the best of 10 humans with models, which adds a selection effect.
    • The claim "LLMs are sub-human on architecture" (GPT-6 Astra 38% vs. best human 64%) rests on 22 human items. A 95% CI on 22 items is about ±20 points, and the human mean is 51% overall.
    • The abstract also says humans "understand too little about data," but humans were not evaluated on the paired data-flip questions at all.
    • The human setup is not described: time limits, whether humans could run code, and what instructions they received.

    All comparisons should be on the same items, report mean human performance with CIs, and avoid human claims that have no data behind them.

Questions for authors
  1. What fraction of sampled questions survives the 10-seed separation filter, and how does the retained distribution differ from the unfiltered one (e.g., in the learning-rate ratio between candidates)?
  2. How do model rankings and the architecture-vs-optimizer gap change with longer budgets (e.g., 10× steps) or tuned learning rates per candidate?
  3. Why do GPT-4o and Llama 3.1 70B beat most frontier models on architecture-only questions? Do frontier models systematically prefer deeper, residual, or LayerNorm candidates that lose at short budgets?
  4. Can you report human mean accuracy with CIs on the same items as the models, and describe the human protocol (time, tools, instructions)? Were humans evaluated on the paired data-flip questions?
2 comments

We thank the reviewer for the careful analysis and concrete suggestions.

Weakness 1: Does the benchmark mainly measure short-horizon optimization?

We do not fully agree that the scores are a consequnce of frontier models applying real-world priors that are inappropriate for short-horizon regime.

First, training budgets must be interpreted relative to the model and dataset sizes. Our recipes use 256-2,048 steps and 4,096-32,768 training samples seen. Many of the runs already converge within these budgets. Second, each question explicitly specifies the dataset, candidate recipes, optimizer, and budget. Deciding whether prior experience applies to these conditions is itself part of the capability being evaluated. Third, strong models do correctly predict many outcomes in this regime: Sol achieves 76.4% on Main500. The evidence in our response to Question 3 also does not support an explanation based on excessive preference for depth or LayerNorm.

Weakness 2: Novelty and missing related work.

We will discuss Wen et al. (NeurIPS 2025) and LLAMBO (ICLR 2024) and clearly state that our contribution is controlled, synthetic, executable training-outcome prediction.

Weakness 3 / Question 4: Human comparison, uncertainty, and protocol.

Figure 1 identifies the human evaluation as a fixed 50-question subset. On these same items (22 architecture, 16 optimizer, 12 mixed), the human mean is 51.0% (95% CI: 43.8%-58.2% across ten participants). The best score is 66.0%; Opus 5, Sol, and GPT-4o each score 64.0%, and V4 Pro scores 68.0%. As also explained in our response to Reviewer tGMv, we will revise the headline comparison to state that top models achieve scores comparable to the best human score on the same questions.

All ten participants have published at leading AI conferences. They predicted which recipe gives the best test metric, with no time limit, only pen and paper, and no internet, code execution, LLMs, or correctness feedback.

Question 1: Filter survival rate and distribution shift.

In a question-forming pipeline run, 204,064/464,944 (43.9%) candidate triples entering the ten-seed separation test survived. For the max/min learning-rate ratio, the median remains 10, while the lower quartile shifts from 1 to approximately 3.33 among passing triples. This changes the retained distribution, but does not invalidate the target capability: predicting execution-grounded outcomes for explicitly specified training recipes.

Question 2: Longer budgets and learning-rate tuning.

We evaluated four representative models on 60 fixed questions (20 per type) at 1x and 10x budget, keeping datasets, candidate recipes, learning rates, and seeds fixed:

Model1x overall10x overall10x architecture10x optimizer
GPT-5.6 Sol85.073.360.080.0
Claude Opus 586.763.345.075.0
DeepSeek V4 Flash71.761.750.065.0
GPT-4o60.053.350.065.0

Sol overtakes Opus at 10x budget; the other relative rankings remain unchanged. Optimizer accuracy remains higher than architecture accuracy for all four models, so the architecture gap persists with longer training.

Question 3: Do frontier models overprefer depth, residuals, or LayerNorm?

On pure-MLP questions where each attribute varies, all six examined models (Claude Opus 5, Claude Sonnet 5, Gemini 2.5 Pro, Gemini 3.1 Pro, GPT-4o, GPT-5.6 Luna) select maximum depth and LayerNorm less often than the winners do. Opus selects maximum depth on 52/124 items versus 78/124 actual winners, and LayerNorm on 46/68 versus 63/68. Some models show a slightly stronger preference for residual connections (Opus: 82/108 selections versus 67/108 winners). These descriptive patterns do not support a universal depth/LayerNorm explanation.

Thank you for the detailed response and the additional experiments.

I am satisfied with the plan to discuss Wen et al. and LLAMBO and to reposition the contribution; please also revise the "first benchmark" statement in the contribution list. The same-item human comparison, the CI, and the protocol description address most of my concerns about the human study. I also accept the Question 3 evidence: models select maximum depth and LayerNorm less often than the winners do, so I withdraw my suggestion that frontier models lose because they over-apply depth/LayerNorm priors.

Weakness 1 remains open. My main concern was not that explanation, but that outcomes in this regime are largely predictable from an effective-step-size proxy. The response does not address the paper's own evidence for this: the analytical effective-learning-rate policy (78.2%) and logistic regression on configuration features (74.2%) match or exceed every LLM. Two new results in the rebuttal reinforce the concern:

  • The filter shifts the lower quartile of the max/min learning-rate ratio from 1 to about 3.33, so retained questions are enriched for large learning-rate gaps.
  • At 10x budget, accuracy drops by 7–23 points with everything else fixed (e.g., Claude Opus 5 from 86.7 to 63.3). This suggests predictions track short-horizon behaviour rather than a budget-aware understanding of training.

Given this, i will prefer to maintain the current score.

Reviewer_vzuxOpenReview ↗
Rating
3
Confidence
3
Informativeness
1
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces ArchitectureIQ, a benchmark where LLMs and researchers predict which of three training recipes will perform best on a synthetic dataset without running experiments. It examines performance on architecture and optimizer choices, sensitivity to dataset changes, and the effects of additional reasoning. It also explores whether a small knowledge base of model-generated rules can improve these predictions.

Critical strengths
  • I think the research question is important for automated ML research and potentially for RSI. Better intuition about training outcomes could help LLMs choose which experiments are worth running under a limited compute budget. The paper offers a concrete way to study one part of this capability.

  • The evaluation covers a broad range of models. Even include Jev, which was very new at the time of submission.

Critical weaknesses
  • The scope of the benchmark does not match the broader claims about AI researchers' intuition. The task in this paper is to rank three predefined training recipes for small synthetic datasets under a fixed training budget. This captures only a narrow slice of research intuition. I think decisions about representations, feature design, suitable model families, and inductive biases may be more interesting and important.

  • The evidence seems insufficient for some of the conclusions about the limitations of LLMs' model intuition. In particular, "The intuition is empirical, not structured" is a stronger claim than the experiments establish. A lack of consistent improvement from longer CoT does not tell us whether the underlying reasoning is structured. The model could lack relevant knowledge, apply an incorrect rule, or fail to combine otherwise valid principles. More tokens would not necessarily resolve any of these problems. The knowledge-base results also make this distinction less clear. Claude Opus 5 proposes propositions that are subsequently curated into conditional, sometimes quantitative rules, and these rules help weaker models. Empirical knowledge can clearly have structure, so what exactly does "not structured" mean here? Producing these propositions does not establish that the model reliably uses them during prediction, but it does make the broad characterization harder to justify. The paper needs a clearer definition and experiments that distinguish knowledge limitations from difficulties in applying or combining rules.

Questions for authors
  • To what extent do benchmark scores represent model intuition?
  • What evidence distinguishes "not structured" intuition from limitations in knowledge or rule application? How does this interpretation fit with the propositions generated by Opus 5?
  • How general are the KB gains across models? Figure 7 shows a clear overall improvement for GPT-4o, while DeepSeek V4 Flash and Qwen3.5 Flash mostly fluctuate across snapshots despite broadly similar starting performance.
  • How were the ten researchers selected, and what makes them representative of the "top AI researchers" discussed in the paper?
2 comments

We thank the reviewer for the careful assessment and constructive suggestions.

Weakness 1 / Question 1: What aspect of model intuition does the benchmark measure?

ArchitectureIQ studies a controlled experimental setting: predicting which specified training recipe performs best on a given dataset under a stated budget. We agree that this scope does not cover every aspect of model training or research intuition. We will make the scope explicit and narrow overly broad claims in the abstract, introduction, and discussion.

Weakness 2 / Question 2: "empirical, not structured" being too strong a claim.

We agree that "empirical, not structured" is ambiguous and can suggest a stronger conclusion than our results support. Our intended observation is that increasing reasoning effort does not consistently improve performance in this setting, which seems more like an intuition rather than structured knowledge like math. We will replace the phrase with this more precise description and revise the associated discussion accordingly.

Question 3: How general are the KB gains?

The gains are indeed model dependent. Figure 7 shows a clear overall improvement for GPT-4o, while DeepSeek V4 Flash and Qwen3.5 Flash fluctuate. These observations support a narrower conclusion: the supplied knowledge can improve prediction for particular recipient models in this setting. We will replace the broad claim of "large gains for weak models" with a description of these model-specific outcomes, explicitly including the models without a consistent gain.

Question 4: Who were the participants, and what supports the reference to "top AI researchers"?

The ten participants are researchers who have published papers at leading AI conferences. The experimental section describes them as "10 human machine-learning researchers." The reference to top researchers in the abstract and introduction motivates the broader research question; it is not intended as a designation of these ten participants. We will clarify their background in the revised experimental description.

Thank you for your response. The rebuttal has addressed most of my concerns. In particular, I appreciate the more narrowly scoped claims, which are now better aligned with the experimental evidence presented in the paper. Overall, I am satisfied with the clarifications and am happy to maintain my positive score.

Reviewer_tGMvOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper introduces ArchitectureIQ, a benchmark designed to evaluate whether language models and human researchers can predict the outcomes of neural network training experiments before execution. The benchmark contains 500 multiple-choice questions covering synthetic datasets and different training configurations, with ground-truth answers obtained through actual training runs.

Critical strengths
  • The paper studies a interesting capability for AI research agents: predicting the outcomes of training configurations without executing experiments.
  • The benchmark uses actual training outcomes rather than model-based judgments, making the ground-truth labels relatively reliable.
Critical weaknesses
  • In the released benchmark bundle, the question and ground-truth files are internally consistent, but the prediction files are incomplete for several models. The GLM-5.2 discrepancy is particularly serious. The released subset contains 178 correct answers out of 220 valid responses, corresponding to 80.9% conditional accuracy, whereas Table 4 reports 66.0% over 500 questions. To obtain 66.0%, 152 of the missing 280 answers would have to be correct. This is mathematically possible, but it cannot be verified from the release.

  • Model results are reported on the full 500-question benchmark, whereas the best human result is measured on a fixed 50-question launch subset. The question composition is also different. Thus, architecture questions represent 44% of the human subset but only 34% of the full benchmark. Architecture questions are also where the models perform relatively poorly. The reported comparison between approximately 76% model accuracy and 66% best-human accuracy therefore does not establish that models outperform human researchers.

  • Several central results lack sufficiently transparent evaluation accounting. In particular, Figure 7 reports accuracy values that are inconsistent with a single evaluation on the stated 50-question subset, while Table 6 excludes invalid responses from accuracy calculations despite substantial differences in response coverage. These issues make it difficult to assess whether the reported improvements and model comparisons are reliable.

Questions for authors

The authors should provide complete per-question predictions, explicit denominators, and consistent treatment of invalid responses.

3 comments

We thank the reviewer for the careful assessment of our results and evaluation protocol. We answer each weakness pointed out and question raised as below.

Weakness 1: Incomplete predictions and the GLM-5.2 discrepancy.

We are not sure which specific "released benchmark bundle" the reviewer refers to. We would appreciate clarification of the source of the numbers. Nevertheless, we checked the reported results. The GLM-5.2 entry in Table 4 uses low reasoning effort and contains 500 valid responses, of which 330 are correct, giving exactly 66.0% accuracy; the corresponding counts are 67/170 for architecture-only, 142/168 for optimizer-only, and 121/162 for mixed questions, consistent with Table 4. We selected low effort because it achieved the highest accuracy over the full 500-question target set among the settings we tested.

The other main-table scores are also consistent with their underlying per-question records. Across the 17 configurations, 16 have 500 valid responses each; MiniCPM has 497 valid responses and three failures, with its reported 39.0% calculated as 195/500. Our check therefore confirms the reported main-table scores.

Weakness 2: Human and model results use different question sets.

The Figure 1 caption already states that the best human result is measured on a fixed 50-question subset. We nevertheless agree that a direct comparison should use identical questions. On this shared subset of 22 architecture-only, 16 optimizer-only, and 12 mixed questions, Opus 5, GPT-5.6 Sol, and GPT-4o each score 64.0%, and DeepSeek V4 Pro scores 68.0%. The human mean is 51.0%, and the best human score is 66.0%. We will revise the headline comparison to state that top models achieve scores comparable to the best human score on the same questions.

Weakness 3: Evaluation accounting in Figure 7 and Table 6.

We apologize for not making the evaluation sizes clear in the paper. In Figure 7, GPT-4o was evaluated on the full 500-question benchmark: 53.2% and 67.6% correspond to 266/500 and 338/500 correct answers, respectively.

The evaluation sizes differed because of inference costs. Full-benchmark evaluation was affordable for GPT-4o, but evaluating every model, particularly Opus 5, on all 500 questions across the eight KB snapshots exceeded our experimental budget. We will state each model's evaluation size in the revised caption.

For Table 6, some responses hit the token limit at the higher reasoning effort used in the original evaluation. We therefore reran GLM-5.2 and Kimi-K3 at low effort on the same original 50 questions. GLM-5.2 scores 23/50 (46.0%) and Kimi-K3 scores 25/50 (50.0%). We will replace the corresponding Table 6 values with these results in the revision.

Thank you for your response. Regarding W1, I would like to clarify that I had read a similar work before and had some impressions of it. However, since the current submission does not include any code or code appendix, I think the AC can ignore this point during the final evaluation.

There are also several other issues in the paper, similar to those mentioned in W3, which I did not list one by one. In addition, the data inconsistencies, the AI-like writing style, the inconsistent data formats across the main text, tables, and appendix (e.g., Tables 3 and 6) have greatly reduced the reliability of the paper.

I do not deny that this work has an interesting motivation. However, the experimental details, overall writing, and presentation make it difficult for me to give it a higher score. Therefore, I will keep my current rating.

I sincerely hope the authors can improve the data organization, check the consistency of the results, and make substantial improvements to the writing in the next version.

We thank the reviewer for the careful follow-up and for recognizing the interesting motivation of our work.

1. Result consistency and revisions

In response to the initial review, we have carefully rechecked all reported results and clarified the evaluation details in the revised pdf:

  • Main-benchmark results. (Appendix D) We checked our data and concluded that the results are sound. The manuscript now explicitly identifies the GLM-5.2 and MiniCPM configuration and evaluation results.
  • Human–model comparison (Section 3.2). The comparison in the paper now uses the same 50 questions. The conclusion is limited to comparable performance on this shared subset.
  • KB evaluation (Figure 7). The revised caption specifies that GPT-4o uses all 500 questions, while the other three models use 50 questions. It also clarifies that curves evaluated on different sets are not direct same-question comparisons.
  • Hard50 evaluation (Table 6, Figure 9 and Table 7). For GLM-5.2 and Kimi-K3, we now report new low-effort evaluations on the same 50 questions.

Regarding the mention of Tables 3 and 6, Table 3 describes the composition of the 500-question main benchmark, whereas Table 6 reports model accuracy on the separate 50-question Hard50 set. Their captions and surrounding text already specify their experimental settings clearly. If the concern refers to other differences in format or content, we would appreciate clarification so that we can respond precisely.

We believe these changes make the evaluation settings explicit and should address the reviewer's concerns.

2. Writing and AI assistance

Regarding "AI-like writing style", the initial manuscript draft was written entirely by the authors. For manuscript writing, AI was only used to polish portions of the text. The abstract and introduction in the final version were written entirely by the authors without AI polishing.

Could the reviewer point us to the passages that appear AI-like and explain which aspects of the wording or presentation are problematic? We would welcome concrete examples and suggestions so that we can improve them directly.

We would appreciate the reviewer's assessment of the revised manuscript.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.