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Under review as a conference paper at ICLR 2027

CBM-Scientist: Agent-driven Automated Concept Bottleneck Model Design

Abstract

Automated research agents hold significant promise for accelerating machine learning research, yet their utility in designing inherently interpretable neural networks remains understudied. We introduce CBM-Scientist, an agent-driven framework for automated concept bottleneck model (CBM) design. Agents iteratively propose, implement, and evaluate model and training changes, using experimental feedback to guide subsequent proposals. We study four proposal strategies across image classification, text generation, question answering, and image generation. Across these settings, agents develop recipes that improve multiple evaluated objectives simultaneously. For example, on AGNews, a loss-constrained recipe improves concept F1 by 15.10 % and steerability by 44.27 % while reducing perplexity from 96.23 to 43.17. Analysis of sprint trajectories shows how agents combine modifications, revisit unsuccessful ideas, and refine training procedures when improvements in one objective do not transfer to others. Together, these findings demonstrate the potential of autoresearch for concept bottleneck model development and highlight the importance of evaluating both task performance and concept use.

Primary area:
interpretability and explainable AI
Keywords:
agentic AI, Autoresearch, Interpretable by Design Models, Concept Bottleneck Models

Reviews

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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.
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Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

The paper introduces CBM-Scientist, which is an agentic framework to automatically improve concept bottleneck models (CBMs). The framework employs an agent to iteratively refine training or model architecture choices of a CBM. Thereby, the agent can modify and evaluate the base CBM and, based on the history of previous exploration and guided by several given target metrics, tries to optimize the smaller details of the CBM structure/training.

Critical strengths
  • The paper proposes an agentic framework to modify a given CBM architecture under certain constraints (e.g., only modifying parts of the model), which can improve the downstream performance of the CBM by optimizing its engineering.
Critical weaknesses
  • While the main idea of using agentic frameworks to automatically construct/improve CBMs is promising, the execution in this paper falls short of what automatic construction should mean in the context of CBMs (and what is claimed in the paper's contributions). There are well-established modules and parts of the CBM pipeline which have important consequences on the way a CBM is set up and works. However, combining these different aspects can be challenging and requires experimentation. But instead of leveraging the knowledge pool that the CBM field has built over the years, the automatic changes in this paper mainly result in small architectural engineering changes, which are mostly not specific to CBMs.
  • The experimental evaluations and setups of the paper lack consistency and are partially insufficient to properly evaluate the introduced method. Some parts of the evaluation are apparently unfinished, and the paper just contains partial results.
Questions for authors

In the following, I have collected several important points/questions regarding the paper, which I would appreciate the authors responding to/clarifying during the rebuttal.

Q1: There are several different agentic approaches introduced, with different performance, but the differences between these agents is never systematically evaluated or discussed. Can the authors comment/discuss why the agents perform differently, and what systematic differences between agentic strategies were?

  • In addition to that, Appendix D.1 even introduces two more variants which are partially evaluated on a part of the datasets, but their performance and implications are never discussed.

Q2: In any automatic setting, it is important to compare cost and benefit, which is not done in this work. There is no discussion on how long this agentic loop should be run. The prompt at the end states it should run until interruption, but stopping criteria are never mentioned/discussed in the paper. Can the authors please discuss the duration of the agentic loop and its connection to performance, in particular regarding the multi-target setting?

Q3: Experimental Evaluation is apparently not finished:

  • Several results in the appendix are missing seeds, or are just outright missing runs.
  • Line 1256 even states, "These are development results, not held-out test results"
  • There are comparisons to other Agents (DeepSeek and Claude Opus, but they are not done on the main experiment results/with the same base CBM configurations, but instead with a different configuration) Q4: Discussion of computational cost of the paper is insufficient:
  • For the estimated costs, the authors report the average cost per candidate in the different settings, but it is unclear how many candidates have been used. Further, for GLM, the authors should, if possible, report the estimated number of GPU-hours and the total number of candidate rounds as well
  • What does it mean that the costs are only computed over completed, scored candidates? Q5: The agents are restricted from changing specific parts of the model and should not change the evaluation setting, but this is only done via prompt. As there are known cases of LLMs doing reward hacking/monkey patching of evaluation functions [1], did this happen during the runs? Q6: Can the authors please position their paper with regard to the field of AutoML? [2] Q7: It is unclear what reported standard deviations are over (l.359 does not state this), and then there is an explicit (and maybe different) standard deviation evaluation in Tab 4. Can the authors please clarify this?

Q8: There is a lot of work on CBMs that introduces different modifications to part of the CBM architecture. Over the years, many different ideas to handle concept annotations, interpretable prediction, input encoding, ... have been proposed. Furthermore, the design space of CBMs has for example been explicitly discussed in [3]. An agentic framework to construct and adapt CBMs should make use of this work. This could, for example, be done by giving the Agents more explicit access to this design space and more freedom to explore it. Additionally, having access to the data and using the data characteristics explicitly to inform the methodological decisions could be helpful there. Can the authors please discuss the current approach in this context?

Q9: In the full experimental evaluation, the results sections just describe the results shown in the tables, but there is no discussion/interpretation of these results given at all. The written text does not have much benefit besides the tables, and compiling more meaningful insights (i.e. why the agentic systems perform better, what changes they made, and what differences there are between the different agentic setups), should be more discussed in the main paper.

Q10: Given that one of the main focus points of CBMs is their interpretability, did the authors perform any investigations into the interpretability of the resulting models, and how it changed compared to the baselines? Also, how many of the changes the agents made were helping/hindering interpretability in general (e.g., as adding more bypass capacity reduces interpretability, improving disentanglement/discretization helps interpretability, ...)?

Q10: There is no Discussion of limitations at all. It would be important to discuss, for example, cost-efficiency, the search space of the agents and proposed changes, the importance of the evaluation criteria, and the lack of interpretation evaluation.

Minor things:

  • Tab 9: Comparing VHCB and the baseline (and the Agents trained on VHCB) is a bit weird, because the latter has a different architecture and setting. From the results, it is not even clear whether VHCB is even better than the baseline.
  • Sec. 4.3: why are the headers called image classification and then the model names for the other two paragraphs? Furthermore, why are sprint internal numbers used in the last paragraph, but not in all the other paragraphs?

[1] Baker, Bowen, et al. "Monitoring reasoning models for misbehavior and the risks of promoting obfuscation." arXiv preprint arXiv:2503.11926 (2025). [2] Zöller, Marc-André, and Marco F. Huber. "Benchmark and survey of automated machine learning frameworks." Journal of artificial intelligence research 70 (2021): 409-472. [3] Knab, Patrick, et al. "What’s in the bottle? a survey and roadmap of concept bottleneck models." Transactions on Machine Learning Research (2026).

10 comments
AuthorsOpenReview ↗

Rebuttal (1/4)

We thank the reviewer for the detailed feedback. As described in the global response, in the new Appendix E, we add experiments and analyses that address many of the points raised. Based on the feedback, we also position our work with respect to the CBM design space of Knab et al. (2026) [3]: in Appendix E.3 (Table 22), we organize the changes the agents made by where they enter the CBM pipeline. We address all of the concerns one by one.

W1: CBM-specific adaptations and connections to prior work

We agree that most proposals are standard changes (76.3% of the 6,650 across the 72 sprints; Table 21, Appendix E.2). This is expected when an agent starts from an existing CBM. But the agents also use what the CBM field already knows: some reuse known CBM techniques, and 14.0% are CBM-specific changes tailored to concept prediction, concept use, or intervention. These changes are not trivial. They span the modules of the CBM taxonomy of Knab et al. (2026), and from them we identify four ideas that, to the best of our knowledge, have not been applied to CBMs before (Appendix E.3, Table 22; Global Response, point 3). We discuss how the agents work within the CBM design space in Q8.

W2: Evaluation completeness and consistency

We agree that parts of the appendix were incomplete at submission, although all results in the main paper were complete. We have now completed the evaluation in two ways. First, four settings (CUB, ImageNet, AGNews, SST2) used test-set feedback during the sprints, so we reran them with validation feedback only and evaluated the selected recipes on a separate held-out test set, as described in the Global Response. Second, we completed the two remaining settings, GSM8K and CUB with human-annotated attributes (the original CBM of Koh et al. (2020)). All reruns use three training seeds (Tables 14 and 15, Appendix E.1). In total, the evaluation covers 72 sprints: 48 are the reruns in Tables 14 and 15, and the other 24, on FinQA and image generation, did not use test-set feedback and are in Tables 2 and 3. We address the specific incomplete results in Q3.

Q1: Comparing proposal strategies across settings

A1: We have expanded the analysis in Appendix E.1 and E.2. Across the nine settings, no single proposal strategy performed best in all of them. In Appendix E.2, we also classify every candidate by its main change, for example as a standard change or a CBM-specific adaptation (a change tailored to concept prediction, concept use, or intervention).

We observe that loss- and architecture-constrained sprints were more likely than self-directed and supervisor sprints to propose CBM-specific adaptations in every model family. All four ideas that, to the best of our knowledge, have not been applied to CBMs before (Appendix E.3, Table 22) also came from these sprints. This does not mean that they performed best. The best-performing recipes often came from other strategies, and which strategy worked best depended on the dataset and metric. We discuss the two additional agent variants of Appendix D.1 in Q3.

Q2: Search duration, stopping criteria, and additional gains

A2: We set a budget of about 100 candidates per sprint and instructed the agent to continue until interrupted. Some sprints ended earlier when the agent stopped proposing changes or repeated failures blocked progress. Others ran slightly longer. We did not use a convergence-based stopping rule.

We reviewed all 24 image-classification sprints and all 16 text-generation sprints. Table R3 shows the results. At each cutoff, we scored the best recipe seen so far using the paper’s standard selection weights. If a sprint ended before a cutoff, we carried its best score forward.

TaskFirst 10First 25First 50First 75First 100
Image classification3.534.715.275.485.80
CB-LLM text generation13.4526.5532.0142.9244.55

Table R3: Best weighted gain over baseline by candidate budget. Δ denotes the recipe score minus baseline for each metric. Rates use a 0–1 scale. Classification = 100 × (0.5 Δaccuracy + 0.25 Δconcept AP + 0.25 Δintervention accuracy). Text generation = 100 × (Δconcept F1 + Δsteerability − 0.005 Δperplexity).

Stopping at 25 candidates would have missed a better recipe by candidate 50 in 20 of 24 classification sprints and 11 of 16 text-generation sprints. The benefit of continuing differed by task. Classification improved more gradually after candidate 25, while text generation still gained substantially between candidates 50 and 75. These results show what earlier stopping would have missed in the recorded sprints.

AuthorsOpenReview ↗

Rebuttal (2/4)

Q3: Completed results and evaluation splits

A3: We would like to clarify that all results in the main submission were complete. In the appendix, we included some extra settings whose results were incomplete at the time of submission. We have now completed them, so in total we have nine settings across three model families (Tables 2 and 3, Section 4, and Tables 14 and 15, Appendix E.1).

  • L1256 : “These are development results, not held-out test results”: This was referring to the GSM8k validation set. (Table 8, Appendix D.2.2). We have completed the experiments and have reported the results on the held out test set in Table 15 (Appendix E.1).

  • We extended the results with DeepSeek and Opus agents on a few settings with Image Generation (Table 9, Appendix D.2). In the one setting we evaluated, a stronger agent (Opus 5) gave better results, which suggests that performance may improve with stronger agents, at a higher API cost (Opus 5 token costs are 2.5× those of Sonnet 5). Testing this more broadly remains future work.

  • We also explored some more agent orchestration variants on limited examples (Figure 4, Table 6, Appendix D.1). We find early experimentation didn’t lead to any significant improvements. We also don’t find any consistent improvement of using supervisor (which is a multi agent framework) over the single agent variants (self-directed , loss, arch ) (Fig 2). Systematic study of different agent orchestrations on CBM Research remains an open question.

Q4: Computational budget and estimated costs

A4: Tables 18–20 (Appendix E.1) now report the number of candidates and the estimated API cost for every sprint, as totals and per candidate. Across datasets, Claude Sonnet 5 sprints produced 3,777 candidates at an estimated USD 8,597.52, and GLM 5.3 sprints produced 2,928 candidates at an estimated USD 6,126.19. These are API-equivalent estimates from published prices: we used a USD 200 Claude Max subscription, and GLM 5.3 was served by an external provider at no charge, so the two should not be compared directly.

completed, scored candidates ?

We are referring to the total number of candidates with a metric score. We agree that is confusing and we will fix this in the revised version.

Q5: Reward hacking and exclusion of affected results

A5: Yes, in two sprints, both run by GLM 5.3. None of the scores from the affected runs were used in our reported results.

  • AGNews text generation (self-directed). Starting with candidate #59, the agent queried the steering classifier during generation and used its score to decide whether to keep generating or to retry an output. The evaluator file stayed unchanged, but its feedback shaped the text it scored. We report candidate #54, which predates this change.
  • CUB image generation (architecture-constrained). The agent used the classifiers that score steerability to choose how to edit each concept. In a separate trial, it tuned the concept predictor's biases against the same classifiers after training.

Q6: Relationship to AutoML

A6: AutoML, surveyed by Zöller and Huber (2021) [2], shares our goal of automating model design but searches over a predefined space of pipelines, algorithms, and hyperparameters. We instead let an LLM agent propose, implement, and evaluate code changes to a CBM, drawing on ideas from other areas of machine learning, combining them, and refining them from feedback. Starting from established CBM baselines, agents improved several objectives together. Most proposals are standard changes (Table 21, Appendix E.2), but agents also proposed four ideas that, to the best of our knowledge, have not been applied to CBMs before, such as a Fourier loss that keeps a concept-edited image close to the original and concept scores that gate the unsupervised features of a generative CB-LLM (Appendix E.3, Table 22).

Q7: Sources of variation in the reported results

A7: In Tables 1–3, 14, and 15, we train the same selected recipe with three random seeds, so the SD measures variation between training runs. In Table 4, we repeat the whole sprint three times. Each sprint can select a different recipe, so the SD measures variation across sprints. We will state this in each caption.

AuthorsOpenReview ↗

Rebuttal (3/4)

Q8: Exploration of the CBM design space

A8: In Appendix E.3 (Table 22), we classify the agents' changes by where they enter the CBM pipeline, following the design space of Knab et al. (2026) [3]. Below, we explain how our setup and the agents' changes relate to its design choices:

  • Concept annotations. We fixed the concept vocabulary and source annotations within each sprint. The agents could still change how they used them during training: for example, an ImageNet agent softened zero targets according to the concept predictor’s own confidence (Appendix E.3, 1(iii), “Confidence-based soft labels”).

  • Interpretable prediction. Following VLG-CBM’s evaluation protocol, each candidate’s concept predictor is frozen and a fresh sparse classifier is fitted at the same budget, so the sparse classifier is fixed. This did not stop a CUB agent from training a temporary classifier on partly corrected concepts to make the concept head more intervenable (Appendix E.3, 1(iv), “Intervention-aware training”).

  • Interpretable generation. In CB-AE or CB-LLM, unlike in VLG-CBM, the decoder and unsupervised pathways are not fixed, and agents could modify them where their strategy allowed. An SST2 agent used the predicted concept scores to gate each unsupervised feature before it reached the decoder (Appendix E.3, 2a(iii), “Gate unsupervised features”). For image generation, a CelebA-HQ agent mapped each concept’s scores to an embedding and appended these embeddings to the decoder input (Appendix E.3, 3(iii), “Per-concept decoder inputs”).

  • Input encoding. Agents could change how backbone features were mapped to concepts. On AGNews, an agent concatenated the current token’s hidden state with the mean of all hidden states through that token (Appendix E.3, 2a(i), “Context-pooled concept head”). In image classification, agents modified the concept predictor in other ways, such as a gated nonlinear residual head (1(i)) and pairwise feature interactions (1(ii)).

Q9: Interpreting the experimental findings

A9: The main paper discusses the results in Sections 4.3 (recurring ideas and their outcomes) and 4.4 (a case study). To add interpretation, we include in the new Appendix E: a comparison of the held-out and original results (Tables 14–16, Appendix E.1), patterns across proposal strategies (Table 21, Appendix E.2), the measured effect of each design choice and case studies of individual agent decisions (Table 22, Appendix E.3), and an extended discussion (Appendix E.4). We will move the important findings into the main paper after the rebuttal.

Q10: Evaluating concept prediction and intervention

A10: We evaluated two aspects of interpretability: how accurately the model predicts the annotated concepts, and how its output responds when those concepts are edited. Across the 56 sprints that measured both, 47 selected recipes improved both mean concept prediction and the intervention metric over their respective baselines (Tables 2, 14, and 15). The remaining 16 image-generation sprints measured steerability without a separate concept-prediction score. All 16 selected recipes improved mean steerability over baseline (Table 3).

The reviewer’s concern about bypassing the bottleneck is visible in the CUB image-generation sprint. An agent gave the decoder a path that carried information about image style through unsupervised features. Adding this path improved reconstruction FID from 68.10 to 9.20, but steerability decreased from 17.12% to 2.08%. Reducing the path to one-quarter strength brought steerability back to 10.50%, while reconstruction FID worsened to 55.27 (Appendix E.3, 3(ii)). The decoder could reconstruct images more faithfully through this path, but edits to the named concepts had less influence on the output.

Reviewer_C2xYOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
3
Soundness
1
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Paper summary

The authors took three standard Concept Bottleneck Model (CBM) setups across different modalities/tasks (image classification, text classification/generation, image generation) and applied an autoresearch harness on top to analyse whether such configurations can be improved by an agent with respect to downstream metrics (accuracy, steerability, etc.). After several iterations, most of the agent configurations (with different constraints) achieved better results than the baseline, either by using optimisation techniques or by relying on existing techniques commonly used in CBMs (e.g. intervention-aware training).

Critical strengths
  • The paper is very easy to read, understand and follow. It is straightforward, free of unnecessary wording, direct to the point, and detailed enough to understand what the authors did, without superfluous details that could confuse the reader.
  • The experiments are extensive. The authors tested the whole methodology on different CBM setups (covering most standard use cases), using different agents and constraints. Well executed.
Critical weaknesses
  • In contrast to the execution, about which I have no concerns, the contribution is weak and feels very incremental. The authors apply autoresearch on top of CBMs to see whether it can improve the metrics of the base models. What is the difference between applying autoresearch to a standard neural network and to a CBM? What challenges would one face, or what doubts would one have, in running such an experiment?
  • Connected to the previous point, the paper leaves me with a feeling of "so what?". I did not find in the paper any learnings or insights that the community can exploit or build upon, beyond what CBMs or autoresearch already provide on their own, that push the research boundary forward.
  • Something interesting to see in such experiments is along the lines of what you discussed in Section 4.4. However, it would be better to categorise what the agent proposed (without giving a long list): for instance, how many times the agent used "optimisation tricks", how many times it simply "reused known CBM techniques" (e.g. intervention-aware training), and when it proposed something "underexplored or new in CBMs", which might be the most interesting part.
  • Minor suggestion: I would rearrange the placement of the figures, as they are often very far from the text that discusses them.
Questions for authors

All the above.

  • Did you use the same test set both for the agent to optimise performance and to evaluate the performance of the final model? I could not find anything in the paper that specifies this, and the only hint, in L911, suggests that this is the case.
  • Are the solutions found by the agent useful across all the tested CBM setups? This would help to understand whether you found something that works well for CBMs in general, or whether the agent is just optimising for that specific setup.
5 comments
AuthorsOpenReview ↗

Rebuttal (1/2)

We thank the reviewer for the positive comments on the clarity of our paper and the extent of our experiments, and for raising three important questions: what our work offers to the community beyond improved metrics, the use of test-set feedback in four settings, and whether the solutions transfer across settings. We address all three with new experiments and analyses in Appendix E, summarized below:

W1 and W2: CBM-specific challenges and lessons from the search

To clarify, CBMs have unique challenges of their own when used with autoresearch:

  • Choosing and jointly optimizing the metrics. The first challenge is deciding what counts as a better CBM. A CBM has many desirable properties (Knab et al., 2026), but a sprint needs a small set of metrics that can be measured for every candidate. We chose three that reflect how a CBM is used: task performance, concept prediction, and the effect of intervention. Improving all three together is not a trivial task. There are other desirable properties, like grounding and concept leakage, as discussed in Knab et al. (2026), which we leave as future work.

  • Making the feedback difficult to exploit. The second challenge is that an agent optimizes whatever score it is given. A metric that is adequate for evaluating a fixed model can become exploitable once it drives the search. For example, CB-LLM does not check the quality of the steered text, so a classifier-based steering score can still rise while the text is incoherent. To prevent this, we added a validity requirement: a candidate is invalid if the perplexity of its steered text exceeds the baseline's steered PPL by more than 60.

To show what the community can learn beyond the final scores, we added an analysis and a set of case studies:

  • Insights from what the agents proposed (Appendix E.2, Table 21). We observe that most of the 6,650 candidates are standard changes (76.3%), but 14.0% are CBM-specific adaptations (defined in W3). The agents therefore do more than routine engineering and hyperparameter tuning: they also propose changes tailored to the CBM, most often in loss- and architecture-constrained sprints.

  • Case studies: where the changes enter the CBM (Appendix E.3, Table 22). We map the agents' main changes, including ones that failed, onto the concept, output, and training modules of the CBM taxonomy of Knab et al. (2026), and report their measured effects. Four of them apply techniques that, to the best of our knowledge, have not been applied to CBMs before, and all four came from constrained sprints.

W3: Classifying the agents' proposals

We thank the reviewer for this suggestion and have added it as Appendix E.2 (Table 21). To understand the ideas the agents proposed, we classified 6,650 candidates from the 72 sprints, including rejected ones, using five categories based on their main change:

  • Standard changes: General-purpose machine learning techniques that are not specific to CBMs, such as changing the learning rate, loss weights, regularization, or model size. These dominate: 81.2% in image classification, 75.5% in CB-LLM, and 68.3% in CB-AE.

  • Changes from the CBM literature: Techniques used in earlier CBM work for the same purpose.

  • CBM-specific adaptations: Changes tailored to concept prediction, concept use, or intervention behavior, with no identified prior CBM method using the same mechanism for the same purpose (12.4%, 16.0%, and 12.0%).

  • Repeated experiments: An unchanged recipe rerun to assess reproducibility or variability.

  • Combined changes: Several changes tested together without a clear primary change.

We observe that architecture-constrained sprints produced the largest share of CBM-specific changes in image classification and CB-LLM (14.9% and 23.3%), while loss-constrained sprints had the largest share in image generation (17.0%). Focusing the agent on one part of the CBM may help it explore that part in more depth, whereas self-directed sprints, which have the most freedom, never had the largest share.

For the "underexplored or new in CBMs" ideas, in Appendix E.3 (Table 22), we show which parts of the CBM design space the agents' proposals address. We identify four ideas (see Global Response, point 3) that, to the best of our knowledge, have not been applied to CBMs before. Interestingly, all four came from loss- or architecture-constrained sprints, in line with Appendix E.2. These ideas are new to CBMs, but they were not the highest-performing ones, which suggests that the most novel ideas do not reliably perform best.

Minor: Figure placement

We will move figures next to the text that discusses them in the revision.

AuthorsOpenReview ↗

Rebuttal (2/2)

Q1: Recipe selection with validation feedback

A1: Thank you for bringing this up. In four of our seven original datasets (CUB, ImageNet, AGNews, SST2), the sprints received test-set feedback. We found no sign that any agent exploited it, but we reran those sprints with validation feedback only. We selected each sprint's recipe on validation data and evaluated it once on a held-out test set, across three training seeds (Tables 14 and 15, Appendix E.1). Table 16 compares the reruns with the original runs:

  • Gains persist. For each dataset, we compare the best recipe in the original and held-out runs, each against the baseline of its own runs. Concept prediction gains are similar or larger in the reruns (concept AP +4.7 → +6.4 on CUB and +7.8 → +9.8 on ImageNet; concept F1 +12.0 → +14.5 on AGNews). Intervention accuracy gains are smaller on CUB (+5.9 → +1.9) and ImageNet (+0.5 → +0.3). Agents again find recipes that improve task performance, concept prediction, and intervention outcomes together: 18 of the 32 sprints on CUB, ImageNet, AGNews, and SST2 (4, 4, 8, and 2 sprints, respectively), and 14 of 16 sprints on CUB-Human and GSM8K (8 and 6 sprints, respectively).

  • Conclusions remain the same. The main claims of the paper hold without test-set feedback: the selected recipes improve task performance, concept prediction, and intervention outcomes together, and no single proposal strategy is best across datasets.

Q2: Transferring recipes across datasets

A2: To investigate this, we retrained each selected recipe on the other datasets of the same model family (Table 17, Appendix E.1). Of the 12 transfers, 9 improved at least one metric over the target baseline and 5 improved all three. We observe that transfer is uneven: some recipes work well on other datasets and some do not:

  • The SST2 recipe improved all three AGNews metrics, while the AGNews recipe improved SST2 concept F1 and steering but failed the steered-PPL validity requirement.
  • The CelebA-HQ recipe improved all three CUB image-generation metrics, while the reverse improved steering at the cost of image quality.
  • Between CUB and ImageNet, which both use GroundingDINO pseudo-labels, both directions improved concept AP with a tradeoff in task or intervention accuracy.
  • Both question-answering transfers (FinQA and GSM8K) improved all three metrics.

Datasets differ in their concepts and distributions, so a recipe that balances these objectives on one dataset may need rebalancing on another. The selected recipes are useful starting points across datasets, but their gains on all three metrics do not always carry over.

Summary

In Appendix E, we show what the agents' proposals teach us about CBMs beyond improved metrics, and that our conclusions hold without test-set feedback and across datasets.

  • What we learn (W1–W3). CBMs have unique challenges of their own when used with autoresearch: the metrics must improve together, and the feedback must be hard to exploit (W1 and W2). In W3, we find that most proposals are standard changes (76.3%), but 14.0% are CBM-specific, and four apply techniques that, to the best of our knowledge, are new to CBMs. All four came from loss- or architecture-constrained sprints (Appendix E.2 and E.3).
  • No test-set feedback (Q1). Rerunning the four affected datasets with a held-out test set, we still find recipes that improve task performance, concept prediction, and intervention outcomes together on every dataset. For example, the selected recipes' concept AP gains are +6.4 on CUB and +9.8 on ImageNet, and the AGNews concept F1 gain is +14.5, similar to or larger than before (Table 16, Appendix E.1).
  • Recipes transfer (Q2). 9 of 12 cross-dataset transfers improve at least one metric and 5 improve all three (Table 17, Appendix E.1).

We believe that we have addressed the reviewer's concerns. Please let us know if you have additional concerns or questions, and we would be happy to discuss further.

Dear Reviewer,

As the discussion period comes to a close, we wanted to check whether our rebuttal addressed your concerns. Please let us know if any still have any questions?. We would also like to note that we made minor changes to Table 22 (Page 41 from manuscript) based on the feedback from other reviewer.

We welcome any further feedback.

Reviewer_BoFSOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

CBM-Scientist uses agents to propose, implement, and evaluate changes to concept bottleneck models. Four proposal strategies cover image classification, text generation, question answering, and image generation. The contribution is an empirical study of automated CBM design, with recipes that improve several objectives and search traces showing how feedback shapes later proposals. Selected recipes are retrained with three seeds, some search settings are repeated independently, and FinQA uses a separate test set.

Critical strengths
  1. With a fixed backbone and sparsity budget, the ImageNet recipe improves ANEC-5, concept AP, and intervention accuracy by 1.52, 7.76, and 0.53 percentage points. Improving these together matters for CBMs, where better task accuracy alone need not mean better concepts or interventions.
  2. The AGNews search trace shows the agent revisiting a candidate with better concept predictions but worse perplexity, then recovering language quality through separate output-layer training. This gives a useful account of how feedback leads to a workable training schedule, beyond reporting the final score.
Critical weaknesses

The AGNews gains cannot be separated from the effect of additional training. After initial training, the selected recipe adds 5,120 concept-head and 20,480 output-layer steps, whereas the baseline trains for one epoch. Different components are updated, so steps are not an exact measure of compute; a baseline given comparable extra optimization is still missing.

Questions for authors
  1. How much of the AGNews gain comes from the new losses rather than extra optimization? Starting from the same baseline checkpoint, compare the original and proposed losses under the same two-stage schedule, trainable layers, batches, and update budget. Report concept F1, steerability, and perplexity to isolate what the new objectives contribute.
  2. Does FinQA’s small correction gain reflect few eligible concept errors or low recovery? Using existing predictions, stratify initially incorrect answers by concept-mismatch count at the prescribed 0.05 threshold; tabulate group sizes and recovery rates for baseline and selected recipe after up to three corrections.
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Rebuttal (1/1)

We thank the reviewer for the positive assessment and for suggesting two useful experiments. We ran both and reported the results below.

Weakness and Q1: AGNews gains beyond additional training

A1: We thank the reviewer for raising this question. The selected AGNews recipe did train for longer than the baseline. Although the instructions specified one epoch, the agent added two stages after the initial training: 5,120 concept-head steps, followed by 20,480 output-layer steps.

To separate the effect of this extra training from the effect of the agent's changes, we ran two controls, both starting from the baseline checkpoint and using the baseline losses. One trains both layers jointly for the same extra budget. The other follows the agent's two-stage schedule exactly, with the same trainable layers, batches, learning-rate schedule, and number of updates. Table R1 reports mean ± std over three seeds.

Training conditionConcept F1 ↑ (%)Steerability ↑ (%)PPL ↓
Baseline58.69 ± 0.4326.73 ± 1.4596.23 ± 19.05
Baseline + extra joint training64.05 ± 0.1221.67 ± 0.4213.44 ± 0.82
Baseline + agent's two-stage schedule63.50 ± 0.3940.60 ± 1.9315.91 ± 0.75
Agent's AGNews recipe (Ours)73.79 ± 0.1171.00 ± 0.5343.17 ± 3.53

Table R1: Separating the AGNews gains from extra training. Concept F1 and steerability (%), and perplexity (PPL), mean ± std over three seeds. Both controls start from the baseline checkpoint with the baseline losses.

We observe the following in Table R1:

  • Extra joint training raises concept F1 and lowers PPL, but steerability falls from 26.73% to 21.67%.

  • The two-stage schedule alone raises steerability from 26.73% to 40.60%.

  • Under the same schedule and number of updates, the agent's full recipe raises concept F1 further, from 63.50% to 73.79%, and steerability from 40.60% to 71.00%. These gains come from the agent's changes, not from the extra updates. The baseline controls do reach lower PPL.

This implies the gains are not from the extra training alone. We would like to point out that none of the sprints violated the one-epoch training rule in the AGNews reruns (Table 15, Appendix E.1), and the selected recipes still showed a similar increase in performance. For example, the GLM 5.3 self-directed recipe improves all three metrics on held-out data (concept F1 by 14.5 points, steerability by 45.5 points, and PPL by 81.2, from 98.2 to 17.0).

Q2: Understanding FinQA’s response to concept corrections

A2: The small gain reflects low recovery after correction, not a lack of eligible concept errors.

To check this, we evaluated the baseline and the selected recipes on the 1,147-question FinQA test set, across three training seeds. For each initially wrong answer, we counted how many predicted concepts disagree with the concept labels (threshold = 0.05), and recorded how often correcting up to three of them fixes the answer. Table R2 pools the counts over seeds. Every initially wrong baseline answer has at least one concept error, as do 89.4% of the wrong answers for the GLM self-directed recipe. We define the recovery rate as the percentage of wrong answers fixed.

Concept errorsBaselineGLM self-directed (Ours)GLM supervisor (Ours)
None (cannot be fixed by correction)0% (0/0)0% (0/115)0% (0/19)
1–20% (0/33)0.50% (1/200)4.55% (5/110)
3 or more0.77% (9/1,166)1.55% (12/774)3.61% (39/1,080)
All wrong answers0.75% (9/1,199)1.19% (13/1,089)3.64% (44/1,209)

Table R2: FinQA answers fixed by concept correction. Initially wrong answers are grouped by how many predicted concepts disagree with the concept labels. Each cell gives the percentage fixed by correcting up to three concepts (the recovery rate), followed by the fixed/wrong counts pooled over three seeds. Wrong answers with no concept errors cannot be fixed by concept correction.

Most wrong answers have three or more concept errors, and correcting up to three of them rarely fixes the answer: recovery is 0.75% for the baseline, 1.19% for the self-directed recipe, and 3.64% for the supervisor recipe. Some wrong answers have no concept errors at all (115 and 19 for the two recipes), which concept correction cannot fix.

To the best of our knowledge, this is the first adaptation of the generative CB-LLM of Sun et al. (2025) to numerical question answering with an evaluation of whether concept corrections fix answers. Improving the intervention capability remains an open item.

We believe that we have addressed the reviewer's concerns. Please let us know if you have additional concerns or questions, and we would be happy to discuss further.

Dear Reviewer,

As the discussion period comes to a close, we wanted to check whether our rebuttal addressed your concerns. Please let us know if any still have any questions?. We would also like to note that we made minor changes to Table 22 (Page 41 from manuscript) based on the feedback from other reviewer.

We welcome any further feedback.

reviewer please discuss with author

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Reminder 2

Dear Reviewer,

We wanted to follow up and check whether we have addressed all your concerns. We believe the paper has become significantly stronger after incorporating feedback from all the reviewers and welcome any further feedback. Please let us know if you have any further questions, and we would be happy to discuss them.

Comments on the paper

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Global Response (1/2)

We thank all the reviewers for the valuable feedback. To address the shared concerns, we added a new Appendix E (all rebuttal additions are in blue). It contains three new experiments suggested by the reviewers, an analysis of what the agents proposed, and case studies of their design choices. The new experiments are: (1) reruns of the sprints with validation feedback only, covering six datasets, two of which were only partly complete before; (2) cross-dataset recipe transfer; and (3) a control experiment that separates the AGNews gains from the effect of extra training (see our response A1 to Reviewer BoFS). The analysis and case studies use the sprint logs: we classify what the agents proposed, show where their changes enter the CBM through individual case studies, and report sprint cost. These new results and analysis support the paper's central claims and clarify several points of confusion. We summarize them below.

1. Held-out evaluation and cross-dataset transfer (Appendix E.1).

In four of our original settings (CUB, ImageNet, AGNews, SST2), the agents received test-set feedback during their sprints. The other three settings were not affected: FinQA already used a separate test set, and image generation on CelebA-HQ and CUB does not use test-set feedback. We found no sign that any agent exploited this test set access. To keep the comparison fair, we still reran the four affected settings using validation feedback only. We then evaluated each selected recipe once on a separate held-out test set, with three training seeds (Table 14 for image classification, Table 15 for language modelling). We observe that the conclusions do not change: agents still find recipes that improve all the metrics together in 18 of the 32 reruns.

In Tables 14 and 15, we also complete two settings from Appendix D.2 (Table 7 for CUB-Human, Table 8 for GSM8K): 8 of 8 CUB-Human sprints (Table 14) and 6 of 8 GSM8K sprints (Table 15) improve all three metrics. In total, we have 72 sprints (9 settings x 4 proposal strategies x 2 models). Of these, 41 sprints improved all three metrics in the final evaluation.

We also observe that recipes transfer between datasets. We retrained each selected recipe on the other datasets of the same model family. Of these 12 transfers, 9 improve at least one metric over the new dataset's baseline and 5 improve all three (Table 17). In addition to this, we report the estimated cost of each sprint, in total and per candidate (Tables 18–20). Together, these results indicate that the gains do not come from test-set feedback and that the selected recipes remain useful beyond the dataset where they were found.

2. What the agents proposed (Appendix E.2, Table 21).

To understand the ideas the agents proposed, we classified 6,650 candidates from the 72 sprints, including rejected ones, using five categories based on their main change:

  • Standard changes. General-purpose machine learning techniques that are not specific to CBMs, such as changing the learning rate, loss weights, regularization, or model size.

  • Changes from the CBM literature. Techniques used in earlier CBM work for the same purpose.

  • CBM-specific adaptations. Changes tailored to concept prediction, concept use, or intervention behavior, with no identified prior CBM method using the same mechanism for the same purpose.

  • Repeated experiments. An unchanged recipe rerun to assess reproducibility or variability.

  • Combined changes. Several changes tested together without a clear primary change.

We report the counts for every model family and proposal strategy in Table 21. We find that most candidates (76.3%) are standard changes, as expected, while 14.0% are CBM-specific adaptations. The agents therefore do more than routine engineering and hyperparameter tuning: they also propose changes tailored to the CBM. In every model family, loss- and architecture-constrained sprints (Section 3.3) had the two largest shares of CBM-specific adaptations. Focusing the agent on one part of the CBM appears to push it beyond routine tuning toward changes tailored to the CBM, while greater freedom did not.

AuthorsOpenReview ↗

Global Response (2/2)

3. Exploring the CBM design space (Appendix E.3, Table 22).

To understand what the agents actually changed, we organize their proposals with the CBM taxonomy of Knab et al. (2026), which groups design choices into the input, concept, output, and training modules. Table 22 maps the agents' main changes onto these modules with their measured effects, and in Appendix E.3, we explain each in a case study. From this, we identify four ideas that, to the best of our knowledge, have not been applied to CBMs before. We do not claim that the underlying techniques are completely novel, but their application to CBMs is new. All four came from constrained sprints (two loss-constrained, two architecture-constrained), which follows from the analysis in point 2. For each, we give the idea and the main performance improvement:

  • Concept-controlled gating of unsupervised features (SST2). Predicted concept scores control how much of each unsupervised feature reaches the decoder. In three GLM architecture sprints, the selected recipes improved steerability on SST2 (+5.20%), concept F1 on FinQA (+14.88%), and all three metrics on GSM8K.

  • Fourier loss on concept-edited images (CelebA-HQ). A frequency-domain loss keeps the edited image close to the original. It improved steerability (+1.64%) and lowered both reconstruction FID (34.28 to 29.14) and intervention FID.

  • Discriminator-feature matching for concept edits (CelebA-HQ). The loss matches the average discriminator features of edited and original images. Matching two layers instead of one improved steerability (+1.06%) and lowered both reconstruction FID (36.63 to 34.36) and intervention FID.

  • PCA features in the bottleneck (CUB image generation). The decoder receives the leading directions of variation of the generator's style vectors through unsupervised neurons. Reconstruction FID decreased by 86%, from 68.10 to 9.20, but steerability fell from 17.12% to 2.08%.

Although these ideas are new to CBMs, they involved trade-offs and were not the best-performing recipes. For example, on CelebA-HQ, a recipe built from standard changes outperformed both loss-constrained recipes on all three metrics. The most novel ideas therefore did not reliably produce the best recipes. This is also consistent with the fact that no proposal strategy performed best across settings (Appendix E.1).

4. Extended discussion (Appendix E.4).

We added a discussion in Appendix E.4 of how the study can be extended: giving the agents more design choices to explore, measuring more properties of CBMs, and studying proposal strategies and sprint lengths further.

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