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Under review as a conference paper at ICLR 2027

Circuit Condensation: Post-Training that Concentrates a Behavior's Causal Circuit

Abstract

One approach in mechanistic interpretability explains model behavior through circuits: the components and connections that carry it. Frozen discovery often returns hundreds of edges, making them hard to inspect, compare, or verify exhaustively. We introduce Circuit Condensation, which post-trains models to concentrate behaviors into smaller causal graphs. Each round prunes low-attribution edges and trains a low-rank adapter to match the original through what remains. It keeps the cut only if task accuracy and held-out perplexity remain within tolerance. Across four behaviors and eight models, condensed circuits are smaller than the strongest published frozen-weight baseline in 30 of 32 settings, by 8.1× on average and up to 316×. Repeating the search without weight updates produces larger circuits in 29 of 32 settings, showing that weight updates drive the reduction rather than search alone. For 19 small circuits, exhaustive subset tests show that 11 are exactly minimal and identify removable edges in the rest. Pair ablations reveal dependencies that single-edge tests miss. On indirect object identification, condensation isolates 24 heads, including 17 with documented roles, whereas a matched frozen circuit needs 61 heads, 36 without documented roles. The result is a sufficient subcircuit of the published mechanism rather than a reconstruction of it. The resulting circuit tracks the original model's next-token distribution and, at matched edge count, predicts its errors better than a frozen circuit in 10 of 11 evaluable settings.

Primary area:
interpretability and explainable AI
Keywords:
mechanistic interpretability, circuit discovery, causal circuits, post-training, edge attribution patching, language models

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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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Paper summary

This paper proposes Circuit Condensation, shifting mechanistic interpretability from discovering small circuits in a frozen model to actively making a model's behavior more concentrated and verifiable through post-training. It combines EAP-IG-guided edge pruning, LoRA-based self-distillation, and validation constraints to produce smaller causal circuits while attempting to preserve the original behavior.

I find this a meaningful research direction, supported by substantial experimental and causal analyses. However, several important questions remain, particularly whether smaller circuits imply better interpretability, how faithfully the adapted model preserves the original mechanism, and whether general capabilities are sufficiently retained.

Critical strengths

S1. A meaningful research perspective with genuine interpretability value.

I particularly appreciate the perspective of this work. Mechanistic interpretability has long faced a practical obstacle: discovered circuits often contain hundreds or thousands of edges, making exhaustive causal verification infeasible. So this work resonates with me.

After examining the method, I recognize that its individual ingredients are relatively straightforward: EAP-IG for selecting important causal edges, LoRA for adapting the remaining computation, and accuracy/perplexity constraints for preventing unacceptable behavioral degradation. Nevertheless, I personally believe this is a paper whose value lies primarily in its research formulation and causal evidence, rather than algorithmic complexity and combination. The underlying research question is meaningful and worth pursuing.

S2. Strong experimental design and insightful analyses.

I appreciate the breadth and organization of the experiments, especially the efforts to distinguish the effects of weight adaptation from those of circuit search. The frozen-weight controls, exhaustive subset and pairwise ablations, and IOI mechanistic interventions form a relatively convincing experimental chain.

Importantly, the paper goes beyond reporting circuit-size reductions and demonstrates what smaller circuits enable in terms of causal verification. I find these analyses particularly valuable.

Critical weaknesses

**W1. Does a smaller circuit necessarily imply better interpretability? **

While I appreciate the substantial reductions in circuit size, I think the paper could better distinguish structural compactness from mechanistic interpretability.

Reducing the number of retained edges clearly makes exhaustive verification more tractable, but it does not necessarily make the underlying computation easier for humans to understand. The surviving components may still perform complex operations, and post-training may redistribute computational complexity rather than genuinely simplify it.

I would therefore appreciate stronger evidence connecting the reported circuit-size reductions to improvements in mechanistic legibility, beyond the reduced cost of causal verification. [Q1]

W2. The boundary between model reshaping and explaining the original model remains important.

Circuit Condensation uses LoRA to make a target behavior depend on fewer edges in the adapted model. However, similar outputs do not necessarily imply identical internal mechanisms, as the same behavior can be implemented through different computational pathways.

I recognize that the authors have made a serious effort to address this issue in Section 5.4, and I appreciate the analyses of edge overlap, output agreement, KL divergence, and IOI mechanistic interventions. Nevertheless, these results primarily establish location overlap, behavioral similarity, and partial mechanistic correspondence, rather than full preservation of the original computation.

In particular, the reported 96.5% answer agreement should be interpreted carefully. On tasks such as IOI, induction, and several docstring settings, both models already achieve near-perfect accuracy, so high agreement may arise even when their internal computations differ.

I would welcome more direct evidence of which mechanisms are preserved, which are reorganized, and what this distinction means for the scientific objective of the paper. [Q2]

Questions for authors

I would appreciate the authors' clarification of the following questions. I find the research direction particularly interesting and hope these questions can lead to further insights into the proposed approach.

[Q1] Does circuit condensation improve mechanistic interpretability beyond structural compactness?

The paper uses retained edge count as its primary measure of circuit complexity. This is reasonable for exhaustive verification, but I believe it captures only one dimension of interpretability.

For instance, a 4-edge circuit may still contain several complex or polysemantic MLP blocks. Without further decomposition, such a circuit is not necessarily easier to understand than a somewhat larger circuit with more clearly organized functional components.

Moreover, LoRA updates span multiple attention/MLP projections, adding approximately 0.9%-1.9% of the original model's parameters (Appendix L). This raises the possibility that some computational complexity is redistributed into the surviving components.

I would particularly appreciate more insightful analyses or quantitative evidence addressing the following:

  • Beyond edge count, how much does condensation simplify the actual mechanism, including the number of functionally relevant components and their interactions?
  • Does post-training genuinely simplify the computation, or partly transfer complexity into the retained heads, MLPs, and adapter?
  • Could the authors provide a more detailed mechanistic case study demonstrating what becomes easier to understand, rather than only easier to verify?

[Q2] Original-model mechanistic fidelity.

As discussed in W2, I appreciate the authors' efforts in Section 5.4, but I remain interested in how faithfully the condensed circuit represents the original model's computation.

[Q2.1] Counterfactual and out-of-distribution consistency.

Could the authors compare the original and condensed models on additional matched counterfactual or out-of-distribution inputs? This would help determine whether their behavioral agreement extends beyond the relatively constrained evaluation distributions.

[Q2.2] Direct comparison of causal mechanisms.

Could the authors measure how the causal effects, activation patterns, or information-routing behavior of corresponding edges change before and after condensation? Such evidence would help distinguish preservation of existing mechanisms from newly learned computational pathways.

[Q2.3] What is the ultimate scientific objective?

This is perhaps my most important conceptual question, and I would particularly appreciate the authors' perspective.

Is the goal to obtain a more faithful mechanistic explanation of the original model, or to construct a behaviorally similar but more interpretable adapted model?

I understand that the paper acknowledges this distinction. Nevertheless, I believe a sharper articulation of the intended scientific contribution would strengthen the work considerably, since these two objectives have different implications for mechanistic interpretability.


[Q3] Novelty relative to existing training-based interpretability approaches.

I have a minor question about the novelty positioning and would appreciate a more insightful comparison with two related studies:

I recognize important differences: Draye et al. primarily constrain attention connectivity rather than directly pruning behavior-specific inter-component edges, while Li et al. focus more on task adaptation and learning dynamics than preserving an original model through self-distillation.

Nevertheless, these works already explore the broader idea of reshaping model computation through training to obtain more interpretable subgraphs.

Could the authors clarify what fundamentally new insight Circuit Condensation establishes beyond these approaches? A more direct methodological comparison, and empirical evidence where the evaluation settings can be aligned fairly, would strengthen the novelty argument.

[Q4] Generalization to larger models.

The largest backbone evaluated in this paper has 4B parameters. I understand the substantial computational cost of repeated circuit analysis and post-training, but I would be more confident in the method's generality if the authors could include at least two larger models.

My concern is that larger models may exhibit more complex redundancy, distributed computation, and adaptation dynamics. It would be interesting to see whether the same condensation behavior and causal properties persist at a larger scale.


[Q5] Experimental questions and concerns.

I have several additional questions about the experimental methodology. Please correct me if I have misunderstood any implementation or evaluation details.

[Q5.1] Computational cost and practical benefit.

Appendix G.1 reports a median condensation runtime of 2.95 hours on one A100 GPU, reaching 17.5 hours in the largest settings.

While smaller circuits substantially reduce subsequent verification costs, the initial post-training overhead may outweigh these benefits when only a limited number of analyses are performed.

Could the authors provide a more explicit cost-benefit or break-even analysis, comparing the total cost of condensation and subsequent verification against conventional frozen-model circuit discovery? I am particularly interested in when the proposed approach becomes practically advantageous.

[Q5.2] Reliability of adapted attribution baselines.

EAP-IG and EAP-GP are adapted to the proposed gate space. The implementation audit in Appendix C reports a Spearman correlation of 0.545 between EAP-IG scores and exact single-edge effects on a 325-edge graph.

Although this provides some support for the implementation, it does not establish equivalence to the original attribution methods, particularly given the modified interpolation space.

Could the authors provide stronger implementation validation, or demonstrate that the main comparisons are robust to these methodological adaptations? This would help establish the fairness of the frozen-weight baselines.

[Q5.3] General-capability preservation under independent evaluations.

The controller imposes a 1.05 perplexity-ratio constraint on its capability probe. However, Appendix E.1 reports approximately 9% median perplexity degradation on WikiText-2, with a worst-case ratio around 1.74, alongside a 5-7 percentage-point decline on LAMBADA.

If the same 1.05 threshold were applied to WikiText-2, approximately 18-19 of the 32 settings would exceed it.

I understand that the controller and independent evaluations use different datasets, but this raises an important question: how reliably does the capability gate preserve general capabilities beyond its particular probe distribution?

Could the authors investigate whether stricter or more diverse capability probes change the final circuit sizes and the resulting interpretability-capability trade-off?


Overall assessment.

I find the research perspective and scientific motivation of this paper particularly compelling. The idea of making causal circuits easier to verify through post-training resonates with my view of where mechanistic interpretability research could become more useful.

My remaining concerns mainly involve whether structural condensation translates into deeper mechanistic understanding, how faithfully the resulting circuits preserve the original model's computation, and whether the observed benefits generalize beyond the current evaluation conditions.

I would be very grateful for the authors' responses, especially for insightful explanations and additional empirical evidence addressing these central questions. I remain open to revising my assessment based on how convincingly these concerns are resolved, and I look forward to a substantive discussion.

10 comments
AuthorsOpenReview ↗

Response to Reviewer HeHi (1/4): W1–Q1

Thank you for distinguishing verifiability from understanding the computation. We address both below. New results use seed 11 unless stated; existing results cite their paper sections.

W1. Does a smaller circuit necessarily imply better interpretability?

Not by itself: edge count measures the size of the causal graph, not the complexity inside a head or an MLP. What a smaller circuit buys directly is verifiability: exhaustive subset tests become possible for the 19 circuits, where every matched frozen circuit is too large to enumerate, and all-pairs interaction tests (run on 48 circuits) would need a median 55× more ablations on matched frozen circuits (§5.3). The evidence that goes beyond edge count is under Q1.

W2. Does the 96.5% answer agreement tell us whether the internal computation is preserved?

Similar outputs alone do not establish the same mechanism. We therefore compared edge attributions, attention patterns, and activations before and after condensation (Q2.2). Because the 96.5% answer agreement saturates near ceiling, we also compared per-example answer margins, logit(answer) − logit(foil), with the original model. C1's answer-margin correlation with the original model is lower than the frozen circuit's (median Pearson 0.44 vs 0.69), although the frozen circuit has 6.4× more edges. The full adapted model scores 0.65 (App. P.1).

Q1. Does condensation improve mechanistic interpretability beyond structural compactness?

We address your three sub-questions separately.

(a) Components and interactions. We checked whether pruning edges also reduces the number of components involved. The median per-cell reduction in writer nodes is 5.0× (median counts: 54 for C1, 198 for the frozen circuit; App. P.1). The remaining components still interact: every circuit has interacting edge pairs, with a median 7.4 partners per edge (§5.3). What changes is that all pairs can now be tested.

(b) Is complexity transferred into the retained components and the adapter? Training concentrates updates in the retained components: their output changes are 1.9× as large as those of other nodes, and the adapter's norm concentrates in the modules the circuit uses (App. P.1). To test whether the reduction requires such large changes, we applied the strict setting in Q5.3. Retained-node changes fall 4.3× (relative L2 0.22 vs 0.96 on the same 13 cells), while circuits remain smaller than EAP-IG (App. P.1, P.3). Restricting adaptation to one component type also preserves small circuits: attention-only and MLP-only adapters give 30 and 20 edges on IOI/Llama-1B, against 18 for the full adapter and 741 for EAP-IG (App. P.7).

(c) A case study of what becomes easier to understand. On the newly added Llama-3.1-8B IOI experiment, frozen EAP-IG needs 1,407 edges. C1 has 9 edges, arranged along this route:

embed → MLP 0 → head 5.11 → MLP 8 → head 15.16 → heads 27.5, 27.20 → logits

Head 15.16 reaches layer 27 both directly and through MLP 19, which is the parallel branch.

From the final position, head 15.16 attends to the repeated subject (attention to S2: 0.42 in the original model, 0.91 after condensation). Heads 27.5 and 27.20 attend to the indirect object (0.20→0.80 and 0.21→0.84) and write to the logits. This matches the S-inhibition → name-mover structure of Wang et al., and every edge in it can be tested on its own. The same heads already prefer the same tokens in the original model. Removing any of the first four edges gives chance (0.52), removing head 27.20's output gives 0.68, and the remaining four edges are parallel branches that are individually redundant (0.94–0.96). Five random 9-edge circuits score 0.52. The three MLPs remain undecomposed, as the paper notes, but they form a far more tractable target for feature-level tools than the 1,407-edge frozen circuit. (Revised paper: App. P.1, P.2.)

AuthorsOpenReview ↗

Response to Reviewer HeHi (2/4): Q2.1–Q2.3

Q2.1. Counterfactual and out-of-distribution consistency.

To test whether the agreement extends beyond the original data distribution, we created held-out sets for all 32 cells, with 1,000 examples each. These use unseen names and five unseen templates for IOI, unseen nouns for agreement, unseen identifiers for docstring, and 2× longer contexts for induction (App. P.4).

OOD accuracy (median)OriginalAdapted modelC1 circuitFrozen circuit
All 32 cells0.980.980.850.91
IOI1.001.000.960.96
Agreement0.780.790.820.71
Induction0.900.960.850.84
Docstring1.001.000.760.98

The adapted model stays within 0.05 of the original in 31 of 32 cells. The C1 circuit does so in 19 of 32, the same count as the frozen circuit. C1 is better on agreement (all 8 cells) and worse on docstring, where three circuits fail on unseen identifiers (Gemma-3-1B 0.62, Gemma-3-4B 0.11, Qwen3-1.7B 0.25, against 0.98–1.00 for the frozen circuits).

Counterfactual inputs. We also scored each circuit under three corruption constructions it was never trained with (a different template, another example's prompt, unrelated text). C1 degrades about as much as the frozen circuit: 0.69 vs 0.65, 0.69 vs 0.67 and 0.24 vs 0.25 (medians, 32 cells). Neither circuit is corruption-independent (App. P.8).

Q2.2. Direct comparison of causal mechanisms before and after condensation.

We compared the original and adapted models on the same edge sets, separating the three measurements you ask about. Results are medians across 32 cells unless stated (App. P.1).

Causal effects. We measured both estimated edge importance and whether the retained edges can carry the behavior together. EAP-IG scores correlate at Spearman 0.86 before and after training. With the adapter removed, C1's edges reach only 0.34 accuracy on the original weights (full model: 0.98). Training therefore makes this set sufficient on its own. These tests compare attribution estimates and circuit-level sufficiency; they do not measure the exact change in each edge's individual causal effect.

Activation patterns. We compared the same components' output activations on the same clean inputs before and after training. Relative L2 change is 1.36 vs 0.76 for retained versus other components. The retained components therefore change more, even though their edges were already important in the original model.

Information routing. On IOI, we measured whether the retained heads still attend to the indirect object or the repeated subject. The before-and-after attention scores correlate at Pearson 0.93 (0.86–0.996 across 8 models). On GPT-2 (seed 11), 19 of the 27 C1 heads have roles in Wang et al., including all 3 Name Movers and all 4 S-Inhibition heads, and none changes its preferred target. This shows similar routing on IOI, though not identical computation.

Two more results show where the circuit comes from and where training acts. Median containment of C1's edges in the original model's frozen circuit is 100% (all edges in 17 cells, at least 90% in 26 of 32), and their median rank is in the top 1.0% of the original EAP-IG ranking. Also, 83% of the adapter's update norm lies in the 55% of modules C1 uses. So C1 is built from pathways the original model already relies on, and training makes them sufficient: the original model's own frozen circuit needs a median 6.4× more edges (App. P.1).

Q2.3. What is the ultimate scientific objective?

Our goal is your second option: an adapted model whose target behavior can be verified through a small circuit, with measured links to the original. Under the strict setting, median WikiText-2 perplexity rises by 0.8% across 32 cells; the full adapted model's answer margins correlate at 0.98 with the original across the 13 audited IOI and agreement cells (App. P.1, P.3). Understanding this model is useful in its own right, as in work on weight-sparse transformers (Gao et al., 2025) and sparse-attention models (Draye et al., 2025). We also test what it tells us about the original: which pathways were already important and how training makes them sufficient. The revised abstract and §1 state this goal, with the evidence in Q2.2 above.

AuthorsOpenReview ↗

Response to Reviewer HeHi (3/4): Q3–Q5.1

Q3. Novelty relative to Draye et al. and Li et al.

We agree that both papers already explore reshaping computation through training. Our contribution is more specific: concentrating one existing behavior into a circuit small enough for exhaustive causal tests, while measuring what changes relative to the original model.

  • Draye et al. add a behavior-agnostic sparsity constraint on attention between token positions. We concentrate the inter-component graph of one named behavior. After condensing one behavior, frozen discovery finds circuits for it with 2–16× fewer edges, while the other three stay at a median 1.0× in all twelve off-target directions (§5.5).
  • Li et al. grow a subgraph while a model learns a task under a task loss. We start from a model that already performs the behavior and distill it toward its own outputs under an accuracy and capability gate, so the goal is preservation.
  • What we add beyond both is evidence about the resulting circuit: exhaustive subset and pair tests (§5.3), and a measurement of what the circuit keeps of the original model (§5.4 and the audit above).

A direct empirical comparison with Draye et al. needs their sparse-attention models; we found no released checkpoints. The closest analogue we can run, joint L0 training of gates and adapter on our graph, returns an admissible circuit in 12 of 32 cells, 5 of them smaller than C1 (App. F.3).

Q4. Generalization to larger models.

We added Llama-3.1-8B and Qwen2.5-7B on IOI, using the same protocol as the smaller models (App. P.2):

ModelGraph edgesFrozen EAP-IGC1, seed 11C1, seed 22C1, strict setting (Q5.3)
Llama-3.1-8B34,8811,40793456
Qwen2.5-7B23,5771,942116112101

Sealed-test accuracy is 0.96–0.98 for every C1 entry (EAP-IG: 0.94 and 0.95). The reduction holds at twice the size of our previous largest model, between 17× and 156×. The two Qwen seeds agree closely; on Llama-8B the stopping point varies with the seed (9 vs 34). The causal checks carry over as well: on both models, five random circuits of C1's size are at chance, and the edge-by-edge results for Llama-8B are under Q1(c). (Revised paper: App. P.2.)

Q5.1. Computational cost and practical benefit: when does the approach pay off?

We timed the complete frozen EAP-IG pipeline (ranking, budget sweep, test) on 15 cells and logged wall-clock and peak memory for condensation, one A100 each (App. P.6).

Frozen EAP-IGCondensation
Runtime, median (range)10.8 min (1.7–33)2.95 h (0.33–17.5), paper setting, App. G.1
Llama-8B / Qwen-7B runtime31 / 20 min24.3 / 9.9 h
Llama-8B / Qwen-7B peak memory47 / 41 GB30 / 25 GB

Whether this pays back depends on the analysis that follows. The runtimes above are measured; the totals below are estimates. They include producing the circuit, assume 200 examples per circuit evaluation, and use the per-cell wall-clock of our strict-setting runs, which are slower (median 6.4 h), so they understate condensation's advantage.

  • Attribution only: frozen discovery is cheaper (at the median, a condensation run takes about 16× as long).
  • One exact drop-one pass (cost grows with k): condensation is cheaper end to end in 5 of 15 cells, those with large frozen circuits (IOI/Qwen3-4B: 31 h vs 78 h).
  • All-pairs test (cost grows with k²): cheaper in 14 of 15 cells, usually by orders of magnitude (Llama-8B: an estimated 46 h vs about 14,000 h). The exception is IOI/Gemma-3-4B, whose frozen circuit already has 8 edges.
  • Exhaustive subsets (2^k): feasible only after condensation (§5.3).

So condensation is worth its cost when the goal is exhaustive verification, and not when a ranked edge list is enough. (Revised paper: App. P.6.)

Reviewer_ddihOpenReview ↗
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Paper summary

Existing circuit discovery methods primarily search for faithful circuits in models with fixed weights. However, task-relevant computation may be distributed across many components and connections, limiting how much improved search alone can simplify the resulting circuits. This paper introduces Circuit Condensation, which treats circuit findability as a trainable model property. Through iterative edge ranking, pruning, and healing, the method trains LoRA adapters while keeping the base-model weights frozen, aiming to concentrate a specified behavior into a smaller causal subgraph.

Critical strengths
  1. Improving circuit findability is a worthwhile research direction in mechanistic interpretability.

  2. The authors transparently report failure cases, residual redundancy, suboptimal endpoints, and computational costs.

Critical weaknesses
  1. The framework involves substantial procedural and computational overhead, requiring repeated attribution scoring, edge pruning, adapter optimization, and validation. A systematic runtime comparison with the attribution-based baselines is missing.

  2. The controller relies on a held-out validation set to accept pruning proposals and determine when to stop. Its applicability when such validation data are unavailable remains unclear. Moreover, because the training, validation, and test splits share template and lexical pools, the evidence for generalization under distribution shift is limited.

  3. EAP-IG and EAP-GP are adapted to gate space, but numerical equivalence to the original implementations has not been established. This leaves uncertainty about whether the baseline results faithfully reflect the performance of the published methods.

  4. The experiments lack direct comparisons with closely related approaches, particularly sparse post-training and Edge Pruning.

  5. The paper lacks ablations on LoRA rank, the choice of adapted projection matrices, and restricting adaptation to selected layers or modules.

Questions for authors
  1. Since closed edges receive activations from corrupted prompts during healing, how sensitive are adapter optimization and the resulting circuits to the choice of corruption construction? Appendix C specifies the task-specific corruptions, but robustness to alternative constructions remains unclear.

  2. The evaluation focuses on token-level behaviors measured using restricted-choice accuracy at a single answer position. Can the framework be evaluated on more complex, multi-token generation tasks?

  3. The frozen-weight baselines identify circuits in the original model, whereas Circuit Condensation identifies circuits in an adapted model. How should circuit-size comparisons across these different models be interpreted, particularly when assessing faithfulness to the original model’s computation?

  4. Exhaustive subset enumeration establishes minimality only among subsets of the returned circuit, under the specified evaluation protocol. It does not rule out a smaller faithful circuit using edges elsewhere in the full graph. Could the authors clarify this distinction and discuss whether such alternative circuits can be assessed?

5 comments
AuthorsOpenReview ↗

Response to Reviewer ddih (1/3): W1–W3

Thank you for the specific requests. We address each below with new comparisons and ablations. New results use seed 11 unless stated; existing results cite their paper sections.

W1. How much does condensation cost compared with frozen attribution methods?

We timed the complete frozen pipeline on 15 cells using one A100 per run, then compared the cost of producing and testing the circuits (App. P.6).

Frozen EAP-IG (rank + sweep + test)Condensation
Runtime, median (range)10.8 min (1.7–33)2.95 h (0.33–17.5), App. G.1
Llama-8B / Qwen-7B runtime31 / 20 min24.3 / 9.9 h
Llama-8B / Qwen-7B peak memory47 / 41 GB30 / 25 GB

At the median, a condensation run takes about 16× as long as a frozen run (measured). Whether it pays back depends on the analysis that follows. In estimated end-to-end cost (producing the circuit plus testing it, at 200 examples per circuit evaluation, using the per-cell wall-clock of our slower strict-setting runs), condensation is cheaper for an all-pairs test in 14 of 15 cells (Llama-8B: about 46 vs 14,000 hours) and for a single drop-one pass in 5 of 15, the cells with large frozen circuits; for attribution alone, the frozen method is always cheaper. (Revised paper: App. P.6.)

W2. Does the controller need validation data, and do the circuits generalize beyond the shared templates and vocabulary?

Validation data. All four tested circuits pass the sealed-test bar without held-out acceptance data and remain smaller than EAP-IG. We accepted cuts on training examples and evaluated once on the sealed test set (App. P.7). The circuits are 1–6× larger than in the paper. All headline arms, including frozen baselines, use the same 2,000-example validation split to select endpoints (§4.3):

CellEdges (accept on train)Sealed-test accuracyTest barPaper C1 (3 seeds)EAP-IG
IOI / GPT-2950.9700.91754–71343
IOI / Llama-1B1120.9950.95017–27741
Agreement / Qwen3-0.6B1,5470.8120.7391,0541,628
Induction / Gemma-1B30.9300.8223849

Distribution shift. We created new test sets for all 32 cells, with 1,000 examples each: unseen names and five unseen templates for IOI, unseen nouns for agreement, unseen identifiers for docstring, and 2× longer contexts for induction (App. P.4).

OOD accuracy (median)OriginalAdapted modelC1 circuitFrozen circuit
All 32 cells0.980.980.850.91
IOI / Agreement1.00 / 0.781.00 / 0.790.96 / 0.820.96 / 0.71
Induction / Docstring0.90 / 1.000.96 / 1.000.85 / 0.760.84 / 0.98

The adapted model stays within 0.05 of the original in 31 of 32 cells. The C1 circuit does so in 19, the same count as the frozen circuit. C1 is better on agreement (all 8 cells) and worse on docstring, where three circuits fail on unseen identifiers (Gemma-3-1B 0.62, Gemma-3-4B 0.11, Qwen3-1.7B 0.25, against 0.98–1.00 for the frozen circuits). (Revised paper: App. P.4, P.7.)

W3. Do the gate-space adaptations faithfully reproduce the published attribution baselines?

For EAP-IG, we checked both agreement with the official library and whether the integration path affects circuit size (App. P.5):

  • Official library. On GPT-2 IOI with identical batches and metric, our implementation of the original input-interpolation EAP-IG matches the official eap library (Hanna et al.): Pearson 0.999 over all 2,041 edges, identical top-71 edges, largest deviation 2.9% of the top score.
  • Does our gate-space adaptation change the result? We re-ran the baseline in all 32 cells with the original path. Median size ratio to our path: 1.00 (smaller in 7 cells, larger in 9, equal in 16). C1 is smaller than the original-path baseline in 30 of 32 cells (8.3× geometric mean), as in the paper.
  • Shared attribution code: C1 vs C0 (7.4×, 29 of 32 cells) runs identical attribution code in both arms (§5.2). (Revised paper: App. P.5.)

EAP-GP. Our implementation follows the published equations and is labeled as such. No released code is available for a numerical comparison; the headline baseline is EAP-IG (App. P.5).

AuthorsOpenReview ↗

Response to Reviewer ddih (2/3): W4–Q1

W4. How does condensation compare with Edge Pruning and sparse post-training?

Edge Pruning style. We trained hard-concrete L0 edge masks on frozen weights with our graph, splits and selection rule, using 8–10 penalty strengths per cell. The table gives the smallest circuit that reaches the accuracy bar (App. P.5).

CellLearned masksC1EAP-IG
IOI / GPT-220371343
IOI / Llama-1B23518741
IOI / Qwen3-0.6B1,0232534,745
Induction / Gemma-1B1,0993849
Docstring / Llama-1B5514801,058
Agreement / GPT-2568595343
Agreement / Llama-1Bnone reach the bar2631,058

Learned masks are a strong frozen baseline and beat EAP-IG in four cells. C1 is smaller in 5 of the 6 cells where they reach the bar.

Sparse post-training. Joint L0 training of gates and adapter finds an admissible circuit in 12 of 32 cells, 5 of them smaller than C1 (App. F.3); fine-tuning followed by discovery gives circuits 4.7× larger than C1 (§5.2). We found no released checkpoints from Draye et al. Our specificity test shows the difference we can measure: the condensed behavior's circuit shrinks 2–16×, while the other three behaviors stay at a median 1.0× (§5.5).

W5. How much do the results depend on LoRA rank and where the adapter is applied?

We varied rank, adapted modules and layer placement on four cells. Attention-only adapts the Q/K/V/O projections and MLP-only the gate/up/down projections (GPT-2: its fused attention and MLP projections). Edges retained; every entry passes the sealed-test bar (App. P.7).

AdapterIOI / GPT-2IOI / Llama-1BAgr. / Qwen3-0.6BInd. / Gemma-1B
Paper (rank 16, 3 seeds)54–7117–271,0543
Rank 443187383
Rank 64221751,8283
Attention only77301,0833
MLP only100209693
Upper-half layers85261,1173
Lower-half layers6654411,38432
Frozen EAP-IG3437411,628849
  • Robust to adapter type. Rank 4, attention-only and MLP-only adapters stay within about 2× of the paper's endpoints and below EAP-IG; a re-run at rank 16 gives 49 / 26 / 969 / 3, so run-to-run variation is similar in size.
  • Placement matters. Upper-half adapters match the full adapter; lower-half adapters give circuits 10–25× larger on IOI and induction.
  • Rank 64 does not consistently give smaller circuits. (App. P.7)

Q1. How sensitive are adapter optimization and the resulting circuits to the corruption construction?

We scored the same C1 and frozen EAP-IG circuits under three corruption constructions not used in training, across all 32 cells (App. P.8). This tests the trained circuits; we did not retrain the adapter under other corruptions.

Closed edges read fromC1Frozen EAP-IGCells: C1 higher / lower / tied
Training construction0.970.9424 / 5 / 3
A different template0.690.6522 / 8 / 2
Another example's prompt0.690.6722 / 9 / 1
Unrelated text0.240.2516 / 10 / 6

Accuracy is the median over 32 cells; the last column splits the 32 cells by which circuit scores higher. Both circuits lose about 0.3 under the in-task alternatives and fall to about 0.25 on unrelated text, so C1 is no more sensitive than the frozen circuit, which keeps about 5× more edges. IOI is the exception (frozen 0.63–0.65 vs C1 0.54). Circuit sizes for both methods are therefore conditional on the training construction (cf. Miller et al., 2024).

AuthorsOpenReview ↗

Response to Reviewer ddih (3/3): Q2–Q4

Q2. Can the framework be evaluated on multi-token generation tasks?

We have not evaluated condensation on multi-token generation. All four behaviors are scored at a single answer position. This is the usual setting for circuit discovery: Sun (2025) notes that almost all mechanistic interpretability studies use tasks with a single-token output, including the IOI setting of Wang et al. (2023) that we build on. Recent work has begun to extend circuit methods beyond this setting: Sun (2025) proposes next-token patching, which scores a patched component by its effect on every generated token, and Haklay et al. (2025) make circuit discovery position-aware, including for inputs of varying length. Condensation would need corresponding choices for its own components: a sequence-level faithfulness metric for the accept/reject gate, a corruption that stays aligned across generated tokens, and edge ranking at more than one position. The masked model can decode autoregressively, but we have not tested whether the controller behaves the same under these choices, and §6 lists multi-token generation as a limitation.

References

  • Alan Sun. Circuit stability characterizes language model generalization. arXiv preprint arXiv:2505.24731, 2025.
  • Tal Haklay, Hadas Orgad, David Bau, Aaron Mueller, and Yonatan Belinkov. Position-aware automatic circuit discovery. In Proceedings of the 63rd Annual Meeting of the Association for Computational Linguistics (ACL), 2025.

Q3. Frozen baselines find circuits in the original model, condensation in an adapted one. How should the size comparison be interpreted?

This is a fair question, and we should have been clearer about it. The size comparison is best read as asking how small a verified circuit for the behavior can be in a model that stays close to the original, rather than how small the original model's own circuit is. The adapted model is still a capable language model, so a verified circuit in it shows how a transformer can carry this behavior; the results below measure how closely that matches the original. Three new results connect the two models (App. P.1).

  • Edge overlap. Across 32 cells, median containment of C1's edges in the original model's frozen circuit is 100%; their median rank is in the top 1.0% of its EAP-IG ranking.
  • The reduction comes from the weight update. On the original weights those edges reach 0.34 accuracy (full model 0.98). Seeding a frozen search in the original model with C1's edges offers no consistent size advantage: same size in 24 of 32 cells, smaller in 2, larger in 6.
  • The small circuit is a property of the adapted model, not of our controller. Plain EAP-IG on the adapted model, with no access to C1, finds a circuit a median 4.3× smaller than on the original (smaller in 29 of 32 cells).

We also tested how much of the reduction survives when we constrain the adapted model more closely. In a strict setting that trains the full model to match the original's outputs, WikiText-2 perplexity changes by 0.8% (median, 32 cells). The full adapted model's answer margins correlate at 0.98 with the original across the 13 audited IOI and agreement cells. The circuits remain smaller than EAP-IG in 25 of 32 cells (details in our reply to Reviewer HeHi, Q5.3; App. P.1, P.3).

Q4. Exhaustive enumeration establishes minimality only among subsets of the returned circuit. Can alternative circuits elsewhere in the graph be assessed?

You are right that these are different claims. "Minimal" in the paper means that no proper subset of the returned circuit is faithful under interchange ablation. It does not rule out a smaller faithful circuit elsewhere in the graph. Since enumerating subsets of 2,000–45,000 edges is infeasible, we used three indirect checks to look for alternative circuits:

  • Across three seeds, 89–95% of the smaller endpoint's edges are contained in the larger one (App. F.4). Independent runs do not land on disjoint circuits.
  • An independent method on the adapted model (the EAP-IG run above) returns a circuit a median 1.3× the size of C1, and equal or smaller in 12 of 32 cells. So C1 is close to what a different search finds, and it is not always the smallest circuit in the adapted model (App. P.1).
  • On IOI/Llama-8B, five random circuits of C1's size are at chance (App. P.2).

Within the returned circuit, the exhaustive tests confirm exact minimality for 11 of the 19 enumerable circuits and identify the removable edges in the other 8, typically 1–3 (§5.3).

Revision. All tables in this response are in the uploaded revision (new Appendix P; changes in blue). Two wording changes follow from your questions: what the size comparison across two models means (§1, §5.4) and what "minimal" means (§5.3). We are glad to answer follow-up questions.

Reviewer_8bHuOpenReview ↗
Rating
2
Confidence
4
Informativeness
2(+1)
Presentation
2
Soundness
1
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Paper summary

The paper proposes a method for learning smaller circuits by repeatedly pruning low-importance edges and retraining a LoRA adapter so that the model preserves the same behavior using a smaller graph. The authors show that this produces substantially smaller circuits than frozen circuit-discovery methods and makes exhaustive subset and pairwise analyses feasible.

Critical strengths
  • There are ablations and controls, which provide insights into how each component in the approach works.
  • The smaller circuits make exhaustive subset testing and pairwise interaction analysis feasible.
Critical weaknesses
  • The central research question is fundamentally flawed. “Can training concentrate a behavior into a smaller circuit?” this is a model compression problem. Once you allow pruning followed by retraining, you are no longer discovering where the behavior originally lives in the model, you are changing the model so the behavior can be carried by a smaller subgraph. Framing the result as a circuit-discovery advance conflates mechanism engineering with mechanism identification.
  • Matching accuracy, next-token distributions, and even error patterns only show behavioral similarity. A compressed or distilled model can satisfy all of these while using a different internal mechanism.
  • Important baselines are missing [1][2]. [1] already learn compact behavior-specific circuits by optimizing masks from the block level down to individual neurons, without adapting the model weights with LoRA. It directly addresses the same scalability and circuit-size problem while preserving the original model. Comparing against coarse edge-pruning methods makes the claimed advantage over “frozen circuit discovery” unreasonable.
  • The cost of this method is unclear since it requires long training time and I did not find information regarding extra memory cost associated with the method.

[1] Multi-Granular Node Pruning for Causal Circuit Discovery

[2] Extracting Interpretable Task-Specific Circuits from Large Language Models for Faster Inference

Questions for authors

N/A

4 comments
AuthorsOpenReview ↗

Response to Reviewer 8bHu (1/2): W1–W2

Thank you for the review. Your question of what the circuit explains once training changes the model led us to state the goal more precisely in the revised abstract and §1, and to add a direct comparison of the original and adapted models (App. P.1). Numbers are new unless a paper section is cited (seed 11, the paper's protocol).

W1. Is this model compression rather than circuit discovery?

We study whether training can make an existing behavior depend on fewer connections, so the resulting circuit can be tested exhaustively. C1 explains the adapted model. To connect it to the original, we test which connections and head roles are retained and how their contributions change. Frozen discovery provides a reference for how many connections are needed before adaptation. The revised abstract and §1 state this goal explicitly.

  • The goal is causal verification, not reducing deployment cost. Condensation removes no model parameters; it makes one behavior depend on fewer connections. After condensing one behavior, frozen discovery finds circuits for that behavior with 2–16× fewer edges, while the three untargeted behaviors stay at a median 1.0× in all twelve directions (§5.5). In a strict setting that also trains the full model to match the original's outputs, WikiText-2 perplexity changes by 0.8% (median, 32 cells), and the circuits remain smaller than frozen EAP-IG in 25 of 32 cells (App. P.3).
  • The retained connections were already important. Across cells, median containment of C1's edges in the original model's frozen EAP-IG circuit is 100%; their median rank is in the top 1.0% of its ranking (App. P.1).

W2. Similar answers do not show that the model uses the same internal process.

To look beyond output agreement, we compared edge attributions, attention patterns, and activations in the original and adapted models, using the same edge sets (32 cells, medians; App. P.1).

What stays similar:

  • Edge importance. The original and adapted models give similar edge-attribution rankings (Spearman 0.86 over all edges).
  • IOI head roles. Per-head attention to the indirect object versus the subject correlates 0.86–0.996 between the two models (8 models). On GPT-2 (seed 11), 19 of 27 C1 heads have roles in Wang et al., including all Name Movers and all S-Inhibition heads, and none changes its preferred target.
  • The IOI intervention. Swapping the signal carried by the S-Inhibition heads flips the answer as Wang et al.'s algorithm predicts in 0.93 of pairs for C1, against 0.65 for the unmodified model (§5.3, App. H.1).

What training changes: with the original weights, C1's edges reach only 0.34 accuracy (full model 0.98). Training makes those edges sufficient to carry the behavior on their own. The retained components change 1.9× more than the rest.

These tests connect C1 to pathways already important in the original model and show how training changes their contributions. (Revised paper: App. P.1.)

AuthorsOpenReview ↗

Response to Reviewer 8bHu (2/2): W3–W4

W3. How does condensation compare with MGNP and García-Carrasco et al.?

Thank you for both references, which the revised paper cites (§2). Both return node sets: which heads, MLPs or neurons to keep, but not which connections between them carry the behavior (MGNP lists this as a limitation). Our unit of analysis is the edge, and every verification test in the paper removes individual connections: exhaustive subset tests, pairwise interaction maps and single-edge ablations. A node set does not define these tests, and counting every connection among the kept nodes as part of the circuit would overstate its size, so node and edge counts are not directly comparable. We therefore compare in two ways.

A learned-mask baseline under our protocol. MGNP optimizes hard-concrete L0 masks on frozen weights with corrupted-activation patching. We ran the edge-level counterpart of that objective (Edge-Pruning style) on our graph, splits and selection rule in 7 cells, with 8–10 penalty strengths each (App. P.5).

CellLearned masks, frozen weightsC1EAP-IG
IOI / GPT-220371343
IOI / Llama-1B23518741
IOI / Qwen3-0.6B1,0232534,745
Induction / Gemma-1B1,0993849
Docstring / Llama-1B5514801,058
Agreement / GPT-2568595343
Agreement / Llama-1Bnone reaches the bar2631,058

Learned masks improve on EAP-IG in four cells, and C1 is smaller in 5 of the 6 cells where they reach the accuracy bar.

Node-level comparison with MGNP's reported IOI results. These use MGNP's own data and metric, so they are indicative only (App. P.5).

IOIMGNP: attention heads kept (reported)C1: attention heads
GPT-2 small34 of 14427
Llama-3.2-1B58 of 51211
Llama-3.1-8B92 of 1,0244

Accuracy is 0.96 for MGNP and 0.96–0.98 for C1. On Llama-3.1-8B, MGNP also keeps 23 of 32 MLP blocks, and C1 uses 3. On the two Llama models, masking with frozen weights keeps 5× and 23× more heads than C1. These head counts are consistent with the pattern in our matched-protocol experiments: weight adaptation can produce smaller circuits than frozen search. The methods are complementary, since MGNP's neuron-level masks could be applied inside the few nodes C1 keeps.

García-Carrasco et al. prune heads and MLPs of GPT-2 small with zero or mean ablation to obtain a smaller, faster standalone model. That goal is compression in the sense of your W1. Our model keeps every parameter.

We have not run MGNP itself on our four tasks and metric, so the node-level comparison above is cross-protocol and is labeled as such. (Revised paper: App. P.5.)

W4. How much extra time and memory does condensation require?

On one A100, the full frozen EAP-IG pipeline (rank, budget sweep, test) takes a median 10.8 min (1.7–33, 15 cells) and condensation 2.95 h (0.33–17.5, 96 runs; App. G.1); on Llama-8B / Qwen-7B, 31 / 20 min against 24.3 / 9.9 h. Peak memory is similar: a median 17 GB (max 47) for frozen EAP-IG and 15 GB (max 53, 34 logged strict-setting runs) for condensation, and 47 / 41 GB against 30 / 25 GB on the two large models (App. P.6).

At the median, a condensation run thus takes about 16× as long as a frozen run. It pays back mainly for verification whose cost grows faster than linearly in circuit size. In estimated end-to-end cost (producing the circuit plus testing it, at 200 examples per circuit evaluation, using the per-cell wall-clock of our slower strict-setting runs), an all-pairs test is cheaper with condensation in 14 of 15 timed cells (Llama-8B: about 46 vs 14,000 hours), and exhaustive subset tests are feasible only after condensation (§5.3). For attribution alone, the frozen method is cheaper (App. G.1). (Revised paper: App. P.6.)

Revision. The results in this response are in the uploaded revision (new Appendix P; changes in blue). We are glad to answer follow-up questions.

AuthorsOpenReview ↗

New experiments: the condensed circuit is already necessary in the original model

Thank you again for your review. On whether the circuit explains the original model, we ran three further tests with the original weights (seed 11, the paper's protocol). All three support the claim in our general response that condensation builds on pathways the original model already uses.

Removing C1 from the original model. We turned off only C1's edges (they receive the corrupted-input activation) and kept all other edges on (504 test examples per cell).

Original model, edges turned offIOIAgreementInductionDocstring
None1.000.750.981.00
C1's edges0.520.230.000.00
Frozen EAP-IG circuit0.520.230.000.00
Edges, C1 / frozen (median)44 / 1,207244 / 1,384111 / 1,012435 / 678

Medians over 8 models per task. In all 32 cells, turning off C1 lowers accuracy as much as turning off the whole frozen circuit (within 0.03), with a median 6.4× fewer edges. On IOI/Gemma-3-1B, C1's 4 edges give 0.53 and the 291-edge frozen circuit 0.50. The few edges C1 keeps are thus as necessary to the original model as its full frozen circuit.

Direct effects of all heads (IOI, 8 models, 64 examples). We patched each head's direct connection to the logits in the original model. The heads C1 connects to the logits rank at a median 94th–99th percentile among all heads. Training changes each head's contribution (rank correlation 0.50–0.90), but these heads keep about the same percentile. C1 therefore uses the original model's strongest output heads.

Path patching on GPT-2 (504 examples). Following Wang et al., we patched each S-inhibition head's path into the name-mover layers and each name mover's path to the logits. In both models, all seven Wang et al. heads rank first or second in their layer, in the same order; the median other head has an effect below 0.01. Condensation keeps the known IOI heads in their original roles.

These results show that C1 is built from edges that are, as a set, already causally necessary in the original model and condensation makes them sufficient on their own. This does not show that the original model uses only these edges, since its own frozen circuit needs more edges to be sufficient. We will add these results to App. P.1 and P.2.

As the discussion period draws to a close, we would be grateful to know whether these results and our earlier response address your concerns. We would gladly engage further on any point that remains unclear. Thank you again.

Thank you again for your review. As the discussion period ends today, we wanted to follow up to see whether our response and the additional results address your concerns. We would gladly engage further on any point that remains unclear.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response to All Reviewers: Summary of New Experiments and Revisions

We thank the reviewers for their detailed and constructive reviews. We added experiments addressing the main concerns and revised the paper to clarify the contribution and its scope. The uploaded PDF marks changes in blue and reports the new results in Appendix P. Three questions came up in more than one review, so we summarize them here. Numbers use the paper's protocol (seed 11, 32 task–model cells) unless stated.

1. What does condensation retain from the original model, and what changes?

All three reviews ask this in some form. We ran a mechanism audit that compares the original and adapted models on the same edges in all 32 cells (App. P.1).

Retained:

  • The same edges. C1's edges come from the original model's own frozen EAP-IG circuit (median containment 100%) and typically rank in the top 1.0% of the original model's edges.
  • Similar edge importance. EAP-IG scores over all edges correlate at Spearman 0.86 between the two models.
  • The same IOI head roles. Per-head attention preferences correlate at Pearson 0.86–0.996 across 8 models; on GPT-2, C1 contains all 3 Name Movers and all 4 S-Inhibition heads of Wang et al.

Changed:

  • Sufficiency. On the original weights, C1's edges reach only 0.34 accuracy (full model 0.98); after training they carry the behavior on their own.
  • Where training acts. The retained components change 1.9× more than the rest, and 83% of the adapter's update lies in the modules C1 uses.

Condensation therefore does not move the behavior to new components: it takes pathways the original model already relies on and trains them until they suffice on their own. Revised paper: abstract, §1, §5.4, App. P.1.

2. Do the gains hold with validated and stronger frozen baselines?

  • Official library. On GPT-2 IOI, our EAP-IG matches the official eap library: Pearson 0.999 over all 2,041 edges, and identical top-71 edges (App. P.5).
  • Original integration path. Re-running the baseline with Hanna et al.'s path in all 32 cells leaves circuit size unchanged at the median (ratio 1.00). C1 is smaller in 30 of 32 cells, by 8.3× on average (App. P.5).
  • Learned masks on frozen weights (Edge-Pruning style, 7 cells). They reach the accuracy bar in 6 cells. C1 is smaller in 5 of them (18 vs 235 edges on IOI/Llama-1B) and larger in one (595 vs 568 on agreement/GPT-2; App. P.5).

3. Scale, capability, robustness and cost

  • Larger models. On IOI, Llama-3.1-8B condenses to 9 and 34 edges (two seeds) against 1,407 for EAP-IG, and Qwen2.5-7B to 116 and 112 against 1,942. (§5.1, App. P.2)
  • General capability. Adding a full-model KL term and a broader probe cuts WikiText-2 perplexity drift from 8.5% to 0.8%, and the LAMBADA drop from 6.8 to 1.2 points. Circuits become about 2× larger and stay smaller than EAP-IG in 25 of 32 cells. (§6, App. P.3)
  • Distribution shift. On new test sets with unseen names, nouns, identifiers and templates, the adapted model stays within 0.05 of the original in 31 of 32 cells. The C1 circuit does so in 19 cells, the same count as the frozen circuit. (App. P.4)
  • Corruption construction. Across the three alternative corruption constructions, condensed circuits show similar median accuracy to the larger frozen circuits (0.69 vs 0.65 with a different template; App. P.8).
  • Cost. Frozen EAP-IG takes a median 10.8 minutes and condensation 2.95 hours (measured). In estimated end-to-end cost (producing the circuit plus testing it, at 200 examples per circuit evaluation, using the per-cell wall-clock of our slower strict-setting runs), an all-pairs test is cheaper with condensation in 14 of 15 cells (Llama-8B: about 46 vs 14,000 hours). (App. P.6)
  • Adapter design. The reduction does not depend on a particular adapter: on IOI/Llama-1B, rank-4, attention-only and MLP-only adapters all give 18–30 edges, against 741 for EAP-IG. What matters is placement: adapting only the upper half of the layers keeps the reduction (26 edges), while adapting only the lower half largely loses it (441). (App. P.7)

The added experiments clarify what condensation achieves: small circuits that make causal verification practical, with measured links to the original model and an explicit trade-off between circuit size and capability retention.

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