acceptodds
Under review as a conference paper at ICLR 2027

Judge Circuits Explain Format-Induced Inconsistency in LLM-as-a-Judge

Abstract

LLM-as-a-judge has become the dominant paradigm for grading model outputs at scale, yet the same model assigns systematically different scores when its output format changes (e.g., a – rating vs. a True/False label). Existing diagnoses of these format-induced inconsistencies stop at the input-output level. Using Position-aware Edge Attribution Patching (PEAP), we causally investigate the internal mechanism in five open-weight instruction-tuned models (Gemma-3, Qwen2.5, Llama-3.1) across five judgment tasks. We find that judgments across structured understanding and open-ended preference tasks share a sparse Latent Evaluator sub-graph in the mid-to-late layers; zero-ablating it collapses judgment while damaging knowledge probes substantially less than a random ablation of equal size in architecturally modular models. By structurally decoupling abstract judging from output formatting, we provide a mechanistic account of format-induced inconsistency on the open-weight models we study: a continuous judgment signal computed in the shared trunk is mapped through fragile, format-specific terminal branches. The judgment itself can therefore be read out independently of the requested output format. Our findings imply that benchmark comparisons of judge reliability across formats partly measure the fragile formatting stage, and can understate the quality of the underlying evaluation.

Primary area:
interpretability and explainable AI
Keywords:
circuit discovery, mechanistic interpretability, representation analysis, llm-as-a-judge, model-based evaluation, explanation faithfulness, probing, interpretability, automated evaluation, knowledge tracing/discovering/inducing, hierarchical & concept explanations, causality

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_UQN7OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper studies how LLM-as-a-Judge behavior differs when outputs are requested as different formats. The authors use PEAP to investigate 5 instruction-tuned models across 5 judgment tasks. They identify Latent Evaluator as the circuits shared by different output formats, and Task Formatter as the circuits that are format-specific. Validation includes activation restoration, ablation with knowledge-task controls, cross-task steering, cross-format activation transfer, and robustness checks across data splits, prompt paraphrases, and attribution methods. The results indicate shared judgment-related pathways within the models, but their internal organization and cross-format transfer vary considerably. The authors thus argue that format-specific output routing may contribute to judgment inconsistency.

Critical strengths

The research question is meaningful, and the empirical evaluation is comprehensive. Format-dependent inconsistencies in LLM-as-a-Judge behavior are an important and practical research problem. The authors investigate this issue through extensive experiments across five different models and five tasks. This makes the work potentially valuable as a mechanistic investigation.

Critical weaknesses

W1: The proposed explanations for format-induced inconsistency are not sufficiently justified

The "format-induced inconsistency" stated in the title and emphasized throughout the abstract and introduction is never directly measured. Specifically, the authors do not quantify the actual inconsistency or disagreement between the rating and classification systems used. Furthermore, they do not examine whether the LE readouts exhibit inconsistencies when the actual outputs from different formats disagree. Additionally, the paper provides no TF intervention experiments that would directly support the claim that "... so fixes can target the formatter." In fact, TF is never directly intervened upon. Steering, FTI, and ablation experiments in Appendix I are all conducted on LE rather than TF. FTI flip rates are highly heterogeneous and lack low-rated-source, random-component or same-format controls, and the label-free readout is evaluated only on rating prompts.

W2: The second contribution (functional modularity) is not well established by the current experiments

Knowledge and judgment are evaluated using different interventions on different sets of components: knowledge is assessed through zero-ablation of the merged LE, whereas judgment collapse is assessed through resampling ablation of the top-ranked edges across tasks and formats. Moreover, the random control itself is highly destructive (reducing MMLU accuracy to 20–23% on Qwen2.5-7B and Llama). Thus, causing "less damage than random" does not imply that world knowledge is preserved. In fact, LE ablation reduces PopQA pure recall from 44.7 to 4.7 on Qwen2.5-7B and from 62.7 to 5.7 on Llama. The claimed generality is also broader than the evidence supports: while pairwise overlap suggests shared structure, the only multi-task core, the merged LE, covers only 3 structured tasks and excludes RewardBench and Yelp.

Questions for authors
  • What are the rating-vs-classification disagreement rates per model and task? On disagreeing instances, does injecting the instance's own rating-prompt LE activations into its classification prompt remove the disagreement, and does intervening on the TFs alone reduce it?
  • Can you ablate C_{TF,rate} and C_{TF,class} separately and report both rating and classification performance?
  • Is the judgment representation shared across formats? Please report the similarity between rating- and classification-derived directions at the same token-aligned LE sites, and apply the fixed BDAS-1D readout to classification prompts
  • How large is the core shared by the LEs of the five tasks, including RewardBench and Yelp, relative to a matched null and the split-half ceiling?

  • In FTI and steering, how are sites mapped between the rating and classification templates, which components and positions are injected, and is the per-task or the merged LE used?
  • Which metric is used to trace C_class, given that EV is undefined for yes/no and three-way labels? What counts as a "component" in Tables 1, 15 and 16?
3 comments

Thank you for the detailed review.

We agree with the central point of W1: the submission never measured the inconsistency promised in its title, and it tested the shared set with two formats only. Both are now addressed. We answer your two weaknesses through your six questions.


Q1. Formats disagree in every model

We evaluated identical instances under all three formats in all 25 model-dataset cells. Formats disagree in every model: the median rate per cell is 26%, and 16 of 25 cells exceed 20% (Table 21, App. V.4).

As a first intervention, we inject the shared set from a same-format donor with the opposite label on Qwen2.5-7B MNLI. This is the same-format control you asked for. The classification output moves toward the donor (+1.04 on the score scale, p < 0.001); rating does not respond, which we report.

We did not intervene on the formatter alone. We have therefore removed the sentence that fixes can target the formatter, and the paper now presents FTI as evidence that the injected components can move the output.

Q2. Each format has its own components

With three formats, each format has its own component set next to the shared one in 15 of 17 cells (a median of 4 components per format). These sets are now defined and listed per cell (App. V.1, Table 19). The paper makes no claim about their individual necessity.

Q3. The representation is shared across rating and A–E prompts

A shared set exists in all 17 retraced cells on four models, and 158 of 215 two-format components remain when a third format (A–E letters) is required. Reversing the letter assignment keeps 15 to 19 of 25 components.

We applied the fixed BDAS-1D readout to the other formats on Qwen2.5-7B MNLI: it reads A–E prompts at about 90% accuracy under both letter assignments and does not transfer to classification prompts. The representation is therefore shared across the two ordinal formats, and we state this narrower scope (App. V.5).

Q4. The five-dataset core is small, so we report graded coverage

It is small. With RewardBench and Yelp included, 3 components are shared by all five datasets for Qwen2.5-7B and none for Llama-3.1-8B; 12 and 7 appear in at least three datasets. Against the split-half ceiling, the strict core is also unstable (Jaccard 0.18 and 0.10 between halves), while the three-dataset sets are more stable (0.53 and 0.39).

We now report per-dataset sets with graded coverage and state that the merged LE of the submission covers CoLA, MNLI, and STS-B only (Table 20, App. V.3). A matched null cannot be built under a strict rule, because it requires a second MLP in the same layer.

Q5. FTI uses per-dataset circuits

FTI uses the per-dataset circuits. The merged LE is used only in the knowledge experiments. Forward runs inject the sender components of the rating circuit, and reverse runs those of the classification circuit, so these runs were not LE-only.

We renamed them (§5, App. K) and added the injection sites, the alignment of positions, and the skipped instructions (App. J). Steering likewise uses the top components of the circuit of the source dataset.

Q6. One metric over all valid labels

The classification circuit was traced with 1 + P(second label | two labels), which excluded MNLI Neutral. All new tracing uses the margin of the gold label over all valid labels, including Neutral. A component is an attention head or an MLP that sends at least one circuit edge; this definition is now stated once and used in all tables (§3.1, App. V.1).

W2. Judgment and knowledge now share one intervention

We agree on all three points. Judgment and knowledge were tested with different interventions; the random control was destructive; and "less damage than random" does not mean knowledge is preserved. We removed that wording and now report the absolute drops you cite. We use exactly one intervention, one component set, and one layer-matched random control with up to ten seeds for rating, classification, A–E, and PopQA.

The result is point 3 of our general response (Table 15, App. U.3): in Qwen2.5-7B and Llama-3.1-8B, the LE is necessary for judgment and for recall alike. In Gemma-3-12B, replacing the LE leaves recall unchanged.


We would be glad to hear whether these changes address your concerns, and we are happy to run further checks.

Thank you for the detailed responses, and I appreciate the authors' efforts to conduct additional experiments. That said, my main concern regarding W1 remains unresolved. While the new experiments provide useful evidence of cross-format disagreement and the causal relevance of the identified circuits, they do not isolate the contribution of the TF components from that of the shared components, particularly on instances where the formats actually disagree. This means the central claim that format-induced inconsistency arises from format-specific output routing still appears stronger than what the current causal evidence establishes. Therefore, I will maintain my rating of 2.

Thank you for the follow-up. We agree that the revision does not cleanly isolate the contribution of the format-specific components. We have since run this intervention on the disagreeing instances of three model-dataset cells (Qwen2.5-7B on MNLI and RewardBench, Gemma-3-27B on MNLI) and find that replacing only the format-specific components of a format with their mean makes at most 3.4% of these instances agree (random components of the same type: 0 – 8.0%).

Could you give us one final recommendation on what would make the paper stronger in light of this result?

Reviewer_5GLEOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies the model internals during LLM-as-a-judge tasks using circuit discovery (specifically, using position-aware edge attribution patching from a 2025 ACL paper).

By comparing the circuits produced for the rating task (on a 1-5 scale) vs. for the classification task (same dataset but output format binarized into Yes/No), the authors isolate the intersection called latent evaluator (LE; related to the core semantic judgment) and the task formatters (the other 2 parts, one related to the 1-5 scale, the other to the Yes/No classification task).

This LE sub-graph is analyzed to check it is roughly the "judgment region" through different experiments:

  1. by replacing the region with 0, and checking that judgment collapses (while general knowledge is usually degrading less compared to adding 0 in the same number of regions randomly); results in Tab. 1;
  2. with format transfer injection (Sec. 5), showing LE is the main driver of the judgment for Qwen 2.5, while for other models, this transfer is undermined by "fragile, non-linear terminal routing".

The whole analysis is conducted on 5 datasets and 5 models.

Critical strengths
  • The work is substantial. Circuits are a convenient way to keep the study manageable.
  • The proposed evidence is clear for the Qwen2.5-7B model
Critical weaknesses
  • There are only 2 output formats (binary and 1-5). There are some implications, e.g. l.292, the latent evaluator might include formatting components that are common for the 2 output formats. I also have some additional questions regarding the experimental settings (see questions below)
  • The "fragility" expressed in Sec. 5 might also be explained by inaccuracy in identifying specifically the correct region for judgment.
  • There are too many directions in the last parts of Sec. 5.1 and 5.2. For instance, the important 1D direction tracking is put in App. E, and each paragraph is related to a different appendix. The authors should select which results need to be highlighted. The LE 1D judgment direction (that looks interesting) is never developed in the main paper, while it is apparent in Fig. 1 (bottom), Fig. 2 (right).
Questions for authors

Most important questions

My overall assessment is mainly driven by the 3 weaknesses above. The following questions are important clarifications I need. I don't except an answer to all minor points.

Clarification regarding whether the region is analyzed for each dataset separately or over all datasets at once

The region for judgment seems only analyzed for each dataset separately (except in Sec. 3.2, but it is a separate IoU analysis). In Tab. 1, the identified LE is cross-dataset, while in line 290, the C_{LE} is only done for each dataset separately (cf. "For each dataset" l.269). Are you doing a cross dataset identification? (I agree that each model might behave differently).

Construction of the datasets

  • As I understood there are five datasets (CoLA, MNLI, STS-B, RB, Yelp), each with 1 judgment task initially (e.g. only binary, or only on 1-5 scale). Then the authors extended the datasets in 2 ways: 1. by converting each dataset into both a binary task and a 1-5 task (the 10 prompts are available in App. G) and 2. by building in each case a contrastive case (i.e., replacing the initial ground truth by another ground truth; this is necessary to apply PEAP, see lines 179,180).
  • For the binary case, constructing a contrastive case is clear (permuting Yes and No); for the 1-5 case, I'm not sure about the process for building the contrastive case. Is this process detailed in the paper?
  • In the example provided, the similarity between "A man is playing a guitar" and "A man is playing a flute" is contextual. What is the process for deciding whether the similarity is 4 or 2; is this process objective?

Related to the datasets:

  • The Fig. 2 left is confusing because it does not clarify what is "clean" and "corrupted": a case can only be clean or corrupted once the rating is known, while there is no such rating in Fig. 2 (left).
  • There are numerous appendices, but a single table summarizing an example for each combination can be beneficial.

Presentation

  • Fig 1 (left): There is a missing word for clean and corrupted prompts. The figure under it is not understandable. The other figures (Venn diagram and 2.) are good.
  • In Tab. 1, only existing knowledge is reported. I think it will be useful to report a table including this knowledge retention together with the judgment capability before/after ablation. This could be just a 2x2 matrix for each model: 1. the judgment capability after ablating LE vs randomly, 2. the existing knowledge after ablation LE vs randomly.
  • The definition of a "task" is confusing: the abstract is telling "across five judgment tasks", so use judgment task as a synonym to dataset. In line 111 the term "judgment task" is defined but aggregate the dataset (one among 5) and the format (one among 2: binary or 1-5). The terms "within-task circuit" (l.132) and "cross-task" (l.193) refer to cross-dataset. The easiest fix for clarification would be to talk about datasets (5 datasets) and output formats (2 formats), and to refer to "cross datasets" or "cross format" when necessary.
  • The Section 3.2 is named "the latent evaluator" (LE), but LE is only defined in Sec. 4.1. In Sec. 3.2, the goal is unclear for me: why are the sets only compared 2 by 2, instead of finding a common ground over the 5 datasets?

Minor points

  • line 178-182: one clear formula could help. Important information has been put in the appendix.
  • l.208/210: you are referring to figure that are not in the main paper.
  • line 40: "yet answers "No"" is unclear in this context: No means similar or dissimilar? (This was only clear for me after reading the templates in one appendix).
  • In l.362: the title is "The latent evaluator carries the judgment" but just below the Finding is unrelated: "The task formatter..." and has not been introduced. The following "clearest causal demonstration" is unclear (is it demonstrating the title 5.1 or the Finding 6?)
  • In Tab. 2, the caption could explain how to read each number qualitatively: close to 100% is the expectation, meaning that LE is the driver of the judgment, and the rest is the format.
  • I agree with l.381, the circuit is not 100% clean, but gives a reasonable identification given the observed output.
  • Conclusion contains 2 times "not A but B" shape.
  • Only the pairs of 4 datasets out of 5 are tested in Fig. 5.
  • It could be interesting to check different models from the same family (e.g., many Qwen) to see whether the judgment location is similar among the different models.
  • It's possible to push back on the last FTI part (since the flip rates are showing a positive result for Qwen only, while the other cells have some ~0; and the related explanation is not exact), but I found the study and the discussion interesting.
3 comments

Thank you for the careful review. We ran new experiments for both of your concerns (output format vs. judgment; failed transfer vs. circuit identification) and revised the paper accordingly.


1. The shared set of components holds on under a third output format

We added an A–E letter format and retraced rating, classification, and A–E with one metric. This now covers 17 model-dataset cells on four models. A shared component set exists in every cell, and it stays largely intact when the third format is required: 158/215 two-format components remain (median 10 of 15 per cell).

We reversed the letter assignment, so that A stands for the opposite end of the scale. In four cells, 15 to 19 of the 25 A–E components stay the same. Tracing the same cell twice changes only 1 to 4 components, so the reversal effect is real and the stable part is independent of the specific letters. Details are in Table 19, App. V.2.

2. Metric and format effects are reported separately

Changing only the metric already changes the identified set (for Qwen2.5-7B MNLI, 10 components before and 9 after, with about half in common), so we report three sets side by side: the original one, the two-format set under the new metric, and the three-format set (Table 19).

3. Failed transfer is not explained by poor localization

We compared the transfer rate of every cell with circuit faithfulness and split-half stability. The relation is weak (rank correlations between 0.24 and 0.31). Well-identified circuits still fail: Gemma-3-12B on MNLI has a faithful and stable circuit and transfers in only 3.7% of pairs. What matters most is the model and the number of labels.

We also found that circuit identification is stable in a graded sense: when two halves of the data disagree on a component, it is almost always just below the cutoff in the other half (Tables 19 and 20).

4. Section 5 has been streamlined

We agree that §5.1 and §5.2 pointed to too many appendices. Section 5 is now shorter and has fewer repeated claims, and the 1D judgment direction now has its own paragraph in the main text (§5.2). New result (point 4 of our general response, App. V.5): the direction trained on rating prompts also reads the judgment from A–E prompts, with about 90% accuracy on Qwen2.5-7B MNLI.

5. Is the LE identified per dataset or across datasets?

You asked whether the LE is identified for each dataset separately or across all datasets. The submission used both without saying so. Table 1 uses both, and we apologize the submission did not say so clearly. Table 1 uses one merged LE over CoLA, MNLI, STS-B. All other experiments, including FTI, use the LE of each dataset. A new table states which circuit each experiment uses (Table 22, App. V.6).

6. Contrastive pairs follow the gold labels of each dataset

Every dataset is used in both formats. A contrastive pair consists of two different instances with opposite gold labels, selected for word overlap. For the rating format, the two gold labels are mapped to the two ends of the 1–5 scale. For STS-B this is objective: we use the human similarity scores of the dataset, at least 4 against at most 2.

As you suggested, a new table lists shows one example pair per dataset with its gold targets in every format (Table 23, App. V.7). The Figure 2 caption now states which prompt is clean and which is corrupted.

7. Judgment and knowledge are in one table

We adopt your suggestion of a 2x2 view per model: judgment and knowledge, each after removing the LE and after removing a random set, now with the same intervention for both.

The result is point 3 of our general response (Table 15, App. U.3): in Qwen2.5-7B and Llama-3.1-8B, the LE is necessary for judgment and for recall alike. In Gemma-3-12B, replacing the LE leaves recall unchanged.

8. Presentation changes

We followed your suggestions:

  • "Dataset" and "output format" replace the shifting use of "task".
  • The LE is defined before its first use, the PEAP formula is in the main text, and figure and appendix references are repaired.
  • Figure 1 now shows complete clean and corrupted prompts, and its caption explains the graph below them. The opening example states what "No" means.
  • The heading of §5.1 no longer contradicts its finding, and the TF is introduced in §2 already. The Table 2 caption explains how to read the flip rates.
  • The conclusion is revised.
  • A five-dataset analysis is added next to the pairwise figure (Table 20). The strict five-dataset core is small, so we report graded coverage.
  • On models of the same family: the paper covers two sizes of Qwen2.5 and of Gemma-3, and Table 19 now lists both sizes of Gemma-3 side by side.

Again, we appreciate the very thorough feedback. We would be glad to hear whether these changes address your concerns and are happy to engage in further discussion.

Thank you for the detailed answers. I appreciate the revisions, but they do not change my overall assessment of the paper, which still relies heavily on the appendices. I kept my score unchanged.

Thank you for reading our response and the revision. We accept your point about the appendices and will restructure the paper so that the main text stands on its own. Could you give us one final recommendation on what would make the paper stronger, for example which results you would keep in the main text?

Reviewer_JiVSOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper looks at a weird problem with using LLMs as judges: the same model can give different answers just because you ask it to output the result in a different format. The authors propose decomposing the internal judgment process into a shared Latent Evaluator (LE) and format-specific Task Formatters (TFs). They employ Position-aware Edge Attribution Patching (PEAP) to identify sparse judgment circuits and investigate this decomposition through circuit overlap analysis, causal ablation, subspace steering, and cross-format activation transfer.

Critical strengths
  1. The research problem is clearly important and practically significant. The sensitivity of LLM-as-a-Judge outputs to scoring format remains a highly important topic; interpretability — including that of large language models — has always been a key concern. The authors attempt to explain this phenomenon from the internal computational mechanisms, which holds practical value for understanding the reliability and interpretability of LLM-based judgments.

  2. The LE/TF mechanistic decomposition provides an interpretable research framework. By separating the shared semantic evaluation process from the format-related output process, the authors offer a relatively clear and testable hypothesis for analyzing cross-format inconsistency. This framework extends the research from simple behavioral observation to the analysis of internal computational pathways, and allows the roles of different modules to be verified through targeted interventions. This idea is fairly novel and constitutes the paper's main conceptual contribution.

  3. Multiple methods are used for cross-validation. The authors cross-validate their findings through a range of techniques, including PEAP, LRPEAP, ACDC, zero-ablation, activation transfer, and subspace steering.

Critical weaknesses
  1. The central conclusion lacks direct causal verification on naturally occurring cross-format inconsistent samples. The paper claims that cross-format inconsistency mainly stems from the Task Formatter rather than the Latent Evaluator. However, based on the experiments presented, it does not appear that the authors systematically quantify the proportion of inputs where the same input actually produces conflicting judgments under different output formats, nor do they separately analyze the causal contributions of the LE and TF on these conflict samples. For example, the FTI experiments in §5 inject LE activations from high-rating inputs into another classification input with a low rating, and this operation simultaneously changes both the input content and the output format. The observed flip in the final prediction can only show that the injected activation is capable of influencing the classification result; it does not directly prove that the original cross-format inconsistency comes from the TF.

  2. The functional definitions of the LE and TF rely heavily on the structural intersection of circuit sets, which is insufficient to establish genuine functional separation. The paper defines the intersection of the rating circuit and the classification circuit as the LE, and the set difference as the TF. However, structural sharing does not necessarily imply that the shared components are specifically responsible for abstract evaluation, nor does structural difference imply that the relevant components are solely responsible for output formatting.

  3. The FTI results vary dramatically across models and tasks, posing a challenge to a unified mechanistic explanation. In Table 2, the transfer success rates differ significantly across models. For example, Qwen2.5-7B achieves flip rates of 99.1%, 100%, and 100% on MNLI, STS-B, and RewardBench, respectively; whereas Gemma-3-27B achieves 0.7%, 96.8%, and 5.3% on the same tasks. The authors attempt to explain these differences through output-label competition and the selectivity of formatting modules, but the current evidence remains insufficient. In particular, MNLI also involves a three-class label structure — why can Qwen2.5-7B achieve near-complete transfer while other models almost entirely fail? These results could equally be influenced by differences in LE activation representations, intervention locations, the models' original prediction distributions, and other factors. The paper itself also acknowledges that a failed transfer may imply that the LE representation is format-dependent. Therefore, the current experiments cannot rule out mechanisms different from the authors' primary explanation.

In summary, based on the current experimental results, there appears to be a certain degree of overclaiming, along with some indirect evidence that cannot be counted as direct proof.

Questions for authors
  1. In Section 4.2, the text states that the PopQA cloze probe shows recall drops under LE ablation for Gemma models “but never on Qwen or Llama.” However, Table 14 reports substantial absolute drops for Qwen2.5-7B and Llama-3.1-8B as well, although they are not worse than their random-ablation controls. Can you revise this statement to clarify that Gemma uniquely shows excess damage relative to random ablation, rather than uniquely showing an absolute recall decrease?

  2. On the direct causal role of the TF. For inputs that actually produce cross-format conflicts, can the authors intervene on only the Task Formatter while keeping the Latent Evaluator's activations unchanged, and test whether the final judgment returns to consistency? If modifying the TF can significantly reduce the conflict rate without hurting the original task accuracy, it would more directly support the paper's central hypothesis.

  3. On the cross-model differences in FTI. Why can Qwen2.5-7B achieve a 99.1% successful transfer on MNLI, while other models generally have very low success rates on the same task?

  4. On the functional validity of the LE/TF division. Beyond defining the LE and TF through circuit intersection and set difference, can the authors ablate or replace each of the two component types separately, and compare changes in semantic judgment accuracy, score distributions, and output formats? In particular, why are some early content-processing components classified as TF, while some terminal routing components are classified as LE?

  5. On the adequacy of the ablation controls. Can the authors provide random-ablation controls that simultaneously match network-layer position, component type, and component count, and increase the number of random trials? In addition, can they adopt a consistent intervention granularity across both the judgment tasks and the knowledge probes, so as to more rigorously verify whether the LE possesses a relatively independent evaluation function?

1 comment

Thank you for the careful review.


The corrected statement regarding PopQA is:

Recall accuracy decreases when the LE is removed on all five models. Only the two Gemma-3 models fall below every random-control trial.

For example, Gemma-3-12B drops from 60.3% to 49.7% while random removal leaves 62.9%. Qwen2.5-7B drops from 44.7% to 4.7%, and random removal is equally destructive there. We removed all wording that implied preserved knowledge (§4.2, Table 1, App. U).

1. Natural conflicts are now measured in all configurations

We now measure natural conflicts directly: all 25 cells, identical instances, three formats. The focused cells contain 99 (Qwen2.5-7B MNLI), 243 (Qwen2.5-7B RewardBench), 62 (Gemma-3-27B MNLI), and 55 (Gemma-3-27B STS-B) conflicting instances. A first intervention shows that injecting the shared set from an opposite-label donor moves the classification output on Qwen2.5-7B MNLI (p < 0.001). We did not intervene on the formatter alone, so we removed the suggestion that fixes can target the formatter and narrowed the central claim accordingly.

2. The LE/TF split is structural

Structurally, each format has its own components next to the shared set in 15 of 17 cells, now tested with three formats and four models. We agree that structure alone is not functional evidence (W2).

On your question about early and late components (Q4): the sets are defined by which formats use a component, and depth plays no role in the definition. An early component used by one format only is therefore counted as TF. We removed the wording that tied the LE to content processing and the TF to terminal, late-layer routing (§2), and the paper now states that the split is structural and approximate (§4.1).

Functionally, we replaced the LE with its average activation and measured all three formats and PopQA recall with one random control. The result is point 3 of our general response (Table 15, App. U.3): in Qwen2.5-7B and Llama-3.1-8B, the LE is necessary for judgment and for recall alike. In Gemma-3-12B, replacing the LE leaves recall unchanged.

3. Circuit quality does not explain the differences between models

We tested whether circuit quality explains them. It does not: transfer rates relate only weakly to faithfulness and stability, and Gemma-3-12B on MNLI fails to transfer (3.7%) with a faithful and stable circuit. The model and the number of labels matter most: Qwen2.5-7B transfers in nearly every case, while on three-label MNLI the other four models stay at or below 4%. We do not have a complete explanation for Qwen2.5-7B, and the paper now presents label preferences and label competition as candidates (§5).

4. The random control now matches component type and layer

The original random control drew components anywhere in the model. The new one matches the component type and takes the nearest layer, over up to ten seeds. Judgment and knowledge now use the same intervention at the level of whole components. We report absolute drops and the difference to random side by side (Table 15, App. U.3).

We keep three findings: (1) a shared component set across three formats and four models, (2) format-specific components next to it, and (3) transfer that depends on the output side. We narrow the claims on preserved knowledge, on a five-dataset core, and on a complete account of the formatter.


We are looking forward to hearing from you whether these changes address your original concerns. We can do further checks before the rebuttal period ends.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

We thank all three reviewers. Their main concerns overlap, and we ran new experiments for each of them. All results are in the revised PDF, featuring a new Appendix V.


1. The shared component set holds up under a third output format

We added an A–E letter format and retraced rating, classification, and A–E with one metric in 17 model-dataset cells on four models. A shared set exists in every cell, and 158 of 215 two-format components remain when the third format is required (Table 19, App. V.2).

2. Formats disagree on identical instances in every model

The submission did not measure the inconsistency it explains. We now pose identical instances under all three formats in all 25 model-dataset cells. The median disagreement rate per cell is 26%, and 16 of 25 cells exceed 20% (Table 21, App. V.4).

3. Judgment and knowledge are tested with one intervention

We replace the LE with its mean activation and measure rating, classification, A–E, and PopQA recall against one random control matched in component type and layer (Table 15, App. U.3).

  • In Qwen2.5-7B and Llama-3.1-8B, replacing the LE disrupts everything. Classification and A–E give one answer for nearly every instance, and PopQA recall falls from 42.7% to 0% and from 62.3% to 5.3%. For Qwen2.5-7B this is more than random sets cause (24% to 33% remain). In these two models the LE is necessary for judgment and for recall alike.
  • Gemma-3-12B differs: with its RewardBench LE replaced, rating gives one answer for 99% of instances while recall is unchanged (61.0% against 60.7%). With its MNLI LE replaced, recall is also unchanged (59.7%), and no format collapses to a single answer.

The separation of judgment from knowledge therefore differs between model families. The abstract, the second contribution, and §4.2 now say this, and we no longer describe the LE as specific to judgment.

4. The 1D judgment direction is shared across ordinal formats

The direction trained on rating prompts reads the judgment from A–E prompts with about 90% accuracy on Qwen2.5-7B MNLI, under both letter assignments. It does not transfer to classification prompts. The direction now has its own paragraph in the main text (§5.2, App. V.5).

Changes in the manuscript

  • §2 defines the LE and the TF by which formats use a component, and §4.1 states that the split is structural and approximate.
  • §3.1 gives the PEAP formula, the tracing metric of each format, and one definition of component, node, and edge.
  • §4.2 and Table 1 no longer imply preserved knowledge.
  • §5 names FTI as rating-circuit injection, and App. J lists the injection sites.
  • App. V adds five tables: three-format sets, cross-dataset coverage, disagreement rates, the circuit behind each experiment, and the construction of contrastive pairs.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.