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Different Learning Trajectories, Same Conclusion: An Investigation of LLMs via Differential Warrant Learning

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Abstract

Reasoning traces are increasingly used as training supervision, yet reaching the same conclusion does not imply learning from the same inferential support. We ask whether changing the validity of a critical warrant, the inferential rule that licenses a targeted inference, changes a model’s reasoning behavior and how the resulting learning difference is organized internally when the reasoning instance, target inference, and training exposure are held fixed. To answer this question, we introduce Differential Warrant Learning (DWL), a matched counterfactual training framework that isolates this contrast. Across experiments on four different LLMs, Healthy (valid-warrant) training consistently yields a higher reasoning-sensitive Terminal validity margin than matched Severe (invalid-warrant) training, although the effect size varies substantially across models. Bidirectional activation transplantation further identifies later, prediction-associated representations that causally carry the Healthy–Severe behavioral contrast across all four settings. How this learned difference matures through depth, however, is model-dependent: representational magnitude does not track causal influence on behavior, and the Healthy–Severe representational difference decreases even as its decision alignment and finite causal leverage increase in one model. Across three model settings, independently constructed validity-related directions—built without Healthy/Severe condition labels or the Terminal-margin gradient—recover the predicted model-specific depth ordering and causally steer Terminal-validity behavior. Finally, activation-level causal expression does not determine where Healthy parameters can be productively inserted into the Severe-trained model. Together, these results distinguish representational difference, causal expression, and parameter replaceability as related but non-equivalent properties of the same matched learning contrast.

Primary area:
causal reasoning
Keywords:
Differential Warrant Learning, Causal Maturation, Parameter Replaceability

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_7XWtOpenReview ↗
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Paper summary

The paper introduces a framework for investigating how training LLMs on valid versus invalid reasoning steps affects their behavior. Across four LLMs, training with valid reasoning steps improves a validity margin. The authors analyze how representational differences, activation-patching effects, and parameter-replacement effects vary across network depth. They demonstrate that these quantities exhibit different, model-dependent trends and do not necessarily coincide.

Critical strengths

Investigating the consequences of training on invalid logical steps is an interesting and worthwhile research direction.

The matched training setup allows for a relatively controlled comparison of the effects of valid versus invalid reasoning supervision.

The paper identifies rather different depth-wise trends across three small language models, which is an interesting empirical observation.

Critical weaknesses

The primary problem of this paper is the writing, which makes the main contribution hard to evaluate. Throughout, many sentences are unnecessarily complicated and verbose, and many new terms are introduced (e.g. causal footprint, causal maturation, causal expression, finite causal leverage, directional refinement, prediction-associated representations, validity-related direction, parameter replaceability, causal geometry, and many more), some of which are hard to understand. The abstract is not very helpful to the potential reader as it is overly technical and uses terminology that is introduced by the paper itself (e.g. reasoning-sensitive Terminal validity margin, Bidirectional activation transplantation). The same is the case for the introduction. Some mathematical quantities are not properly defined, e.g. Δhl\Delta h_l

The main behavioral metric, terminal validity margin, measures likelihood preferences over given candidate continuations rather than letting the model produce a reasoning trajectory itself, limiting the conclusions about reasoning capabilities and making the higher terminal validity margin for the healthy training is unsurprising as a direct artifact of the training setup.

The substantially different depth-wise trends across models could have been discussed more.

Questions for authors

Have you considered evaluating generated reasoning on independent, out-of-distribution tasks to test robustness of measured behavioral differences?

Can you provide possible explanations for the substantially different depth-wise trends observed across models?

2 comments
AuthorsOpenReview ↗

Responses to Weaknesses

Thank you for the review. We apologize that some terminology was insufficiently explained. Below we clarify the definitions and their relation to prior work, and present new generation and intervention results.

W1. Writing, definitions, and terminology in prior work

A warrant is the rule licensing an inference. Healthy (H) uses a valid warrant; Severe (S) uses a corrupted warrant that does not justify the target inference. Training examples are matched by their original problem and target inference.

Our contribution is an empirical investigation of three properties of this supervision contrast: differences in internal states, effects of swapping states, and gains from swapping weights. These measurements need not peak at the same layers.

We distinguish established methodological terms from the labels used to describe our experiments:

ExpressionMeaning hereLocationTerminology in cited work
Terminal validity marginValid continuation's mean token log-probability minus the highest score among invalid alternatives.§3, Eq. (11).Our metric; related to logit-difference evaluation in Zhang & Nanda (2024).
Bidirectional activation transplantationCopy H states into S and S states into H in separate runs.§3, Eq. (12).“Activation patching” in Zhang & Nanda (2024); “interchange intervention” in Geiger et al. (2022).
Causal footprint / causal expressionWhere state replacement transfers the donor model's behavioral difference.§§3–4.Our labels for intervention locations/effects; Hase et al. (2023) use “causal tracing.”
Causal maturationChanges in state differences and their effects across layers at a fixed checkpoint.§5.1.Our descriptive label.
Finite causal leverageMeasured score change after an actual state replacement.§5.1, Eq. (14).Our definition of FF, using activation patching.
Directional refinementNormalized state difference shrinks while alignment and intervention effects strengthen.App. E.3.Our descriptive label.
Prediction-associated representationsStates at positions used to score continuation tokens.§3; App. B.5.Our label for the intervened positions.
Validity-related directionA vector contrasting average states for valid and invalid candidates.§5.2, Eq. (19).“Validity direction” appears in Bertolazzi et al. (2026); Eq. (19) defines our construction.
Parameter replaceabilityWhether copying selected H weights into S improves the score.§6, Eq. (20).“Parameter replacement” appears in Sun et al. (2026); our criterion is the resulting score gain.
Causal geometryDistribution of intervention effects across layers and positions.§§4–6.Our descriptive label.

These references use the related methodological terms; the DWL-specific definitions are given above. We will define each term and symbol at first use and simplify the abstract and captions.

W2. Candidate scoring versus generated reasoning

The original margin provides a common measure for comparing internal interventions. Generation tests measure how the supervision contrast affects model-generated answers and proofs.

On the official ProofWriter open-world test split, models generate an answer and supporting fact/rule IDs. For 1,200 provable questions, the checker requires a correct answer and verifies that the cited support derives the claim or its negation, as appropriate. No candidate continuation or gold proof is supplied for the test question.

This checks support sufficiency; the separate paired experiments in Part II check each step of an ordered proof.

Training was expanded to 84,111 instances per condition, approximately 12.6M loss-bearing tokens for Qwen2.5-3B and 13.2M for Qwen3.5. Models with positive mean H–S differences are:

ModelSeedsCorrect answer + sufficient support: H–S
Qwen2.5-3B4+3.21%
LLaMA-3.2-1B3+4.28%
Ministral-3B4+2.92%
Qwen3.5-2B2+22.38%
Qwen3.5-4B1+12.33%

Here % denotes absolute differences between success rates. Means include all completed seeds per listed model; 4B uses one seed. These results extend the supervision contrast to generated answers with verified support.

W3. Model-dependent depth trends

The differing depth profiles are part of the finding. Part II shows how the same supervision contrast produces different patterns of representation change, alignment, and causal influence across models.

AuthorsOpenReview ↗

Questions and Additional Findings

Q1. Generation on independent, out-of-distribution tasks

We added generation on the official ProofWriter test split: 1,200 provable queries from 600 sets of facts and rules, covering depths one to three.

This extends the original ProofWriter candidate evaluation to generated answers and supporting facts and rules. This tests whether models generate correct responses with sufficient evidence.

Paired two-/three-step problems separately test ordered proof generation and stopping.

Q2. Why do depth-wise trends differ across models?

Three factors matter: the size of the change to an internal state, its direction, and how strongly subsequent computation responds to it. A large change can have little effect if it points away from directions that change the score.

In the original notation, RR measures normalized state difference. CC is alignment with the score gradient, the direction of steepest local increase. FF averages the score gain from inserting H states into S and the loss from inserting S states into H.

The layer pairs below were selected on discovery data and evaluated on held-out questions:

Model and layer pairChange in CCChange in FF (nats/token)What changes?
Qwen2.5-3B, L21→L27+0.01582+0.01476Better alignment accompanies a stronger effect.
Ministral-3B, L15→L19+0.00651+0.01695The effect strengthens despite a smaller normalized state difference.
LLaMA-3.2-1B, L10→L15−0.01033−0.00550Alignment and effect weaken after an earlier peak.

Both contrasts have these signs in all three seeds per model (Appendix E, Tables 14–16).

These profiles reflect model-specific combinations of alignment and sensitivity. Architecture and pretraining are plausible contributors, whose separate effects would need to be tested in controlled comparisons.

Additional findings: effects on proof completion

Using separate Qwen2.5-3B checkpoints with matched warrant-text frequencies, we evaluate 600 paired problems across three training seeds. Each pair has the same starting facts and target conclusion but requires two or three rule applications. A complete proof must apply the rules in a valid sequence and reach the correct answer. All % changes below are absolute differences in rates.

1. Better rule selection does not guarantee a complete proof. Given the correct starting fact, the H–S differences are:

Generated behaviorTwo-step problemsThree-step problems
Correct first rule+2.89%+4.33%
Correct answer and complete valid proof+9.17%−7.33%

For the stopping test, we supplied the correct first two steps. Requiring one more rule choice reduced the three-step H–S third-rule gap from −22.56% to −0.50%, and the complete-proof gap from −18.56% to −5.17%. The model chose among six rules; the correct choice was not supplied.

2. Changing internal states changes stopping and proof completion. After the same two-step prefix, we intervened once at L27 on the last prompt token, moving H states toward S, then let the model generate. Premature answering fell by 10.33%, and three-step complete-proof accuracy rose by 5.17% (95% CI [+4.00%, +6.44%]). On two-step problems, where the proof was already complete, the same intervention reduced complete-proof accuracy by 7.50%. Its benefit therefore depends on whether another inference is needed.

3. Alignment explains the stronger L27 stopping effect. We define a stopping score as the log-probability of starting the answer minus that of continuing with a rule. For a single state change of norm aa, the standard first-order relation is

=aG_{\mathrm{stop},\ell}C_{\mathrm{stop},\ell}+\epsilon_\ell.$$ Here $G$ is the gradient norm, measuring local sensitivity; $C$ is cosine alignment with that gradient; $\epsilon$ is the difference between the measured effect and this approximation. The original $R$ is normalized state difference, not $a$. With S as recipient and the same norm at both layers, the L27–L21 stopping-score effect is **+0.606 nats**. Decomposing each problem before averaging gives **+1.000 from alignment, −0.364 from sensitivity, and −0.030 from the remainder**. The larger effect comes from better alignment despite lower sensitivity. This single-recipient score change is distinct from the original bidirectional $F$. The interval resamples paired problem groups, keeping the three training seeds fixed. **These experiments connect the original internal analysis to a concrete generation decision: whether to continue a proof or answer. Better initial rule selection can be offset by answering too early.**
Reviewer_YVWPOpenReview ↗
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Paper summary

This paper investigates how the validity of reasoning supervision affects LLM behavior and internal mechanisms when the underlying reasoning problem and target conclusion remain unchanged. The authors introduce Differential Warrant Learning (DWL), a matched counterfactual training framework that varies the validity of a critical inference rule across Healthy, Mild, and Severe conditions. Experiments on four LLMs show that Healthy training consistently improves the Terminal validity margin relative to Severe training, although the effect size varies considerably. Through activation transplantation, representation analysis, validity-direction steering, and parameter replacement, the authors find that the learned differences exhibit a relatively consistent late-layer causal footprint but follow model-specific depth trajectories. They further show that representational differences, causal influence, and productive parameter replacement locations do not necessarily coincide.

Critical strengths

S1. A well-motivated question with a clean, controlled design. The paper separates reaching a correct conclusion from learning it through valid inferential support. By matching the reasoning instance, target inference, and training exposure, and by using the Healthy–Severe difference rather than the pretrained model as the estimand, DWL is more targeted than comparing training on correct versus incorrect traces.

S2. Different notions of localization are compared within one contrast. The paper measures representational difference, activation-level causal effect, and parameter replaceability on the same learned difference. Ministral-3B illustrates the result most clearly: normalized discrepancy decreases from L15 to L19 while causal leverage increases, and productive replacement occurs upstream at L6–8. This is a useful caution against treating activation or patching maps as editing targets.

S3. Careful protocol and transparent reporting. Hypotheses and layer pairs are fixed on Discovery data before held-out evaluation. Failed and reversed predictions are retained, for example the failed late-MLP replacement in LLaMA and the module-level reversal in Qwen2.5-3B. Same-condition cross-seed controls are reported for both activation and parameter transplants. This level of transparency is uncommon in interpretability work and makes the results easier to calibrate.

Critical weaknesses

W1. Limited methodological novelty and incremental mechanistic findings. DWL offers a useful experimental setup, but the subsequent analyses largely combine established techniques, including activation patching, representation probing, steering, and parameter replacement. Several central conclusions are closely related to prior findings: validity-related representations have already been studied (e.g., Wu et al., 2025; Bertolazzi et al., 2026), and the mismatch between causal localization and effective parameter editing has been reported by Hase et al. (2023). The paper's contribution is primarily a unified empirical comparison, but it remains unclear what substantially new mechanistic understanding is obtained beyond these existing observations.

W2. Incomplete isolation of warrant validity. Although DWL matches the reasoning instances and training exposure, changing a warrant can simultaneously alter its factual correctness, semantic strength, and linguistic properties. For example, replacing ALL with MOST or SOME changes both logical validity and the distribution of linguistic patterns encountered during training. The paper acknowledges these differences but does not provide sufficient controls to separate their effects. In particular, analyzing lexical or structural overlap between training corruptions and evaluation candidates, or introducing validity-preserving perturbations, would help determine whether the observed behavioral differences reflect logical reasoning rather than surface-level preferences.

W3. Limited behavioral significance and generalizability. The primary behavioral evidence relies on the Terminal validity margin, with Healthy–Severe differences ranging from approximately 0.004 to 0.053 across models. The improvement is particularly small for Qwen2.5-7B, and secondary evaluations do not consistently reproduce the same ordering. More importantly, improvements in candidate log-probability margins do not necessarily imply improvements in actual reasoning accuracy or generated reasoning quality. The paper also uses a relatively short continual-pretraining setup (192 steps and approximately 3.15M processed tokens per condition), leaving unclear whether the findings extend to more realistic reasoning-supervision settings such as SFT or RL.

W4. Limited evidence for the specificity and robustness of the proposed causal organization. The consistent late-layer, prediction-associated causal footprint may reflect a general property of training-induced behavioral differences rather than a mechanism specific to warrant validity. Same-condition cross-seed controls do not fully address this possibility; a matched non-validity training contrast would provide a more informative comparison. Furthermore, the proposed causal-maturation patterns are confirmed primarily through selected layer pairs and three training seeds. The independent validity directions are constructed at layers identified by earlier causal analyses, and the crossed-anchor robustness test yields mixed results for LLaMA-3.2-1B. These limitations weaken the evidence for a robust and generalizable depth-wise organization of validity-related learning.

Questions for authors

Is the late-layer footprint specific to warrant validity, or would any fine-tuning-induced difference produce it?

3 comments
AuthorsOpenReview ↗

Responses to Weaknesses

Thank you for the detailed review. We added a validity-preserving training control, expanded-training generation evaluations, and interventions on proof continuation.

W1. Novelty and mechanistic findings

Our contribution is an empirical investigation of how a controlled change in reasoning supervision alters internal computation. Wu et al. (2025) separate and modify content and logic representations; Bertolazzi et al. (2026) examine how validity and plausibility are represented and influence judgments; Hase et al. (2023) compare causal localization with effective editing of stored facts.

DWL asks how learning the same inference and conclusion through different warrants changes the relation between representation, causal influence, and parameter replaceability. In Ministral, the representation difference decreases from L15 to L19 while the activation effect increases, and productive parameter replacement occurs upstream at L6–8. The new experiments further connect the training-induced difference to rule selection and stopping decisions. Part II reports how these decisions affect complete proofs and how alignment explains the layer dependence.

W2. Controlling linguistic and factual differences

The original construction covers 10 corruption families. We added a controlled corpus with 24,112 records per condition and exactly equal frequencies of the same 1,190 warrant texts across Healthy, Valid-Alt, and Severe. Each matched instance fixes the premises, displayed rules, and target conclusion. Healthy and Valid-Alt select different applicable rules; Severe selects a displayed rule whose antecedent is not satisfied for the target subject.

All rules are stipulated premises of the constructed world. Rotation balances warrant-text frequencies, and packing matches sequence lengths and token exposure. Valid-Alt provides a validity-preserving training control. This design controls the marginal warrant-text distribution and tests rule applicability in context; it does not establish that every semantic difference has been eliminated. The controlled Qwen2.5-3B experiments use three training seeds.

W3. Generated reasoning and training exposure

All % changes denote absolute differences in rates.

We evaluated free generation on ProofWriter using joint correctness: a correct answer with sufficient proof support. On 1,200 provable questions, a symbolic checker verifies that the generated answer is correct and the cited facts and rules suffice to derive the target.

The expanded corpus contains 84,111 matched instances per condition, trained for one full pass. Qwen2.5-3B receives 12,660,257 Healthy and 12,599,264 Severe loss-bearing tokens per seed, approximately 12.6M per condition. Qwen3.5 uses its own tokenizer and receives approximately 13.2M per condition. The following models have positive mean H−S differences on the joint metric:

ModelSeedsCorrect answer + sufficient proof: H−S
Qwen2.5-3B4+3.21%
LLaMA-3.2-1B3+4.28%
Ministral-3B4+2.92%
Qwen3.5-2B2+22.38%
Qwen3.5-4B1+12.33%

Values are mean differences across all completed seeds for each listed model; the 4B entry reports one seed.

This joint generation endpoint complements candidate likelihoods by requiring both a correct answer and proof support. The additional runs test increased data and exposure within continued training; SFT and RL are outside the evaluated objectives.

W4. Specificity and robustness

We compare H–S with the H–Valid-Alt validity-preserving training control, matching intervention norms across both contrasts, both layers, and both fact contexts. On 240 held-out paired problem groups, we compare directions from the original context with directions from a fact-swapped context that changes which candidate is valid.

The L27–L21 increase in context dependence is 0.1946 nats/token larger for H–S than H–Valid-Alt, with 95% CI [0.1781, 0.2106]. Seed-specific differences are 0.1485, 0.1972, and 0.2381. Thus, the late-layer context effects differ between the two tested training contrasts under equal norms.

For the original independent validity directions, independence concerns construction without H/S labels or the Terminal-margin gradient. Layer selection uses discovery data and is distinct from that independence claim. We retain the model-dependent depth interpretation.

Reported intervals use paired bootstrap over evaluation problems or theories, with training seeds fixed.

AuthorsOpenReview ↗

Question and Additional Mechanistic Findings

Reviewer's question

Is the late-layer footprint specific to warrant validity, or would any fine-tuning-induced difference produce it?

The H–Valid-Alt control supports an applicability-related contribution. Both contrasts change training, but only H–S changes whether the selected warrant applies. With equal norms, H–S shows greater late-layer context dependence in all three seeds. This conclusion concerns the tested control, rather than every possible fine-tuning contrast.

The following experiments use the controlled Qwen2.5-3B checkpoints, three training seeds, and 600 paired two-step/three-step problems. They provide complementary tests of a stopping contribution, without estimating complete causal mediation.

1. Local rule selection improves, but complete-proof gains depend on depth

All % changes denote absolute differences in rates.

Healthy improves first-rule accuracy over Severe by 2.89% on two-step problems and 4.33% on three-step problems. Yet complete-proof accuracy changes by +9.17% on two-step problems and −7.33% on three-step problems. Here, a complete proof must be valid and reach the correct answer.

The paired problems match the starting fact and target conclusion while varying proof depth. This separates the quality of initial rule selection from the ability to finish a proof.

2. Requiring continuation reduces the three-step gap

We supplied the correct first two steps and compared ordinary generation with a condition requiring one more rule choice. The model selected from six displayed rules; the correct choice was not supplied.

The Healthy–Severe third-rule accuracy gap shrank from −22.56% to −0.50%, and the complete-proof gap from −18.56% to −5.17%. This intervention changes the opportunity to stop while leaving the next rule to the model. It shows that the free-generation deficit includes a substantial continuation component.

3. Internal intervention changes stopping and proof completion

After supplying the correct two-step prefix, we intervened once at L27 on the last prompt token, moving Healthy activations toward Severe, then allowed free generation. On three-step problems, premature answering fell by 10.33%, and complete-proof accuracy rose by 5.17% (95% CI: [+4.00%, +6.44%]). Proof gains were positive in all three seeds.

The same intervention reduced complete-proof accuracy by 7.50% on two-step problems, where the supplied prefix had already completed the proof. Encouraging continuation thus helps when another inference is needed and hurts when the proof is finished. Half-dose L27 intervention improved three-step proof accuracy by 2.44%; full-dose L21 intervention improved it by 1.94%.

We also extracted directions at the initial rule-selection prompt and froze each direction before transfer to the stopping prompt. The bidirectional L27 effect was 3.22% toward the Healthy stopping tendency, with the same sign in all three seeds. Each problem uses its own frozen direction.

4. Directional alignment explains the stronger late-layer effect

The original framework distinguishes normalized representation difference RℓR_\ell, decision alignment CℓC_\ell, and finite intervention effect FℓF_\ell. We apply the same analysis to a stopping score: the log-probability contrast between answering now and continuing with a rule.

For an intervention of fixed norm aa, the standard first-order relation gives

= aG_{\mathrm{stop},\ell}C_{\mathrm{stop},\ell}+\epsilon_\ell.$$ Here, $G$ is the gradient norm, $C$ is the intervention direction's cosine alignment with that gradient, and $\epsilon$ is the finite-intervention remainder. The decomposition quantifies the contributors to the observed effect; the empirical finding is which contributor dominates. With Severe as recipient, the equal-norm L27–L21 effect increases by **0.606 nats**. Decomposing each problem before averaging gives **+1.000 nats from alignment, −0.364 from sensitivity, and −0.030 from the remainder**. Alignment strengthens while sensitivity decreases, explaining the larger late-layer effect in this setting. Intervals use paired problem bootstrap with the three training seeds fixed. The score decomposition explains the intervention's effect on the stopping score; proof accuracy is measured separately by generation. **DWL connects controlled differences in reasoning supervision to changes in internal causal organization and concrete generation decisions, showing that improved local reasoning does not necessarily translate into better complete proofs.**

Thank you for your reply. I’ve decided to keep the grade as it stands. I believe it is consistent with the grading criteria.

Reviewer_W7LdOpenReview ↗
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Paper summary

Overall, the paper investigates an interesting and important problem on understanding what establishes the inferential rule in causal reasoning. They introduce Differential Warrant Learning with the goal to provide a causal investigation of what affects model reasoning.

Critical strengths

The paper has some clear signs of good results. The experiments seem to be well ablated for the considered models (though not necessarily within the model family, see below) and capture a relatively wide range of scenarios.

Critical weaknesses

My biggest problem with the paper is that the language is very hard to parse. A lot of terms are not explained or not referred to, and examples are not given to sufficient detail (there's a brief mention of one in Fig. 1). For example, what is parent reasoning instance, terminal validity, or causal maturation? What does it mean to replace something productively? Even if some of the terms have an existing literature (which, since I'm not an expert in this particular subject, I'm not aware of), it's hard to pin them down because the authors do not provide references nor an explanation. This makes the paper extremely hard to contextualise, especially since in many cases it's unclear what the potential meaning of the results is.

Also, other unclear terms are mentioned, such as finite causal leverage (why finite?) or collateral reasoning benchmarks (the appendix only mentions collateral metrics). You are mentioning the 3B, 7B Qwen models, but further ablations with respect to model size within the family would have been necessary to show any trend between size and capability. For example, for Figure 2, it's unclear what the ranges of the parameter values are. It's unclear whether the analysis was run with multiple seeds or not (some tables do mention multiple seeds).

Also, one more thing: in Appendix A, the human quality audit, you are mentioning their names, though do not define them. This makes the paper's claims especially hard to audit and discern.

I encourage the authors to discuss the causal model, the methodology and assumptions that enables making a causal claim.

Also, the notion of the trajectory is not defined explicitly (my understanding is that it's kind of an evolution within the model itself). Including that would also improve the presentation quality.

All in all, even though I definitely appreciate the authors' intent, many of the details are missing for easy dissemination, which makes my recommendation a reject.

Figure captions are often not self-contained. For example, the Figure 4 caption is not self-contained. I encourage the authors to provide much more detail and clarify the writing style, especially since there is a lot of spacing where they could save some space (I mean the spaces between formulas, etc.).

On a few more things in Figure 1:

  • It's unclear what panels B, C and D are supposed to mean.
  • Explaining in maybe a bit more detail what healthy means, what mild means, and what severe means (Table 1 does not clarify, e.g., what is "locally plausible"?), whether it's a violation that is logically false or whether that indicates some uncertainty without contradicting anything, would clearly improve the paper.
Questions for authors

N/A

3 comments
AuthorsOpenReview ↗

Responses to Weaknesses

We sincerely apologize for not making the manuscript sufficiently accessible to readers less familiar with this area. We will promptly revise the terminology, examples, and figure captions, and distinguish established methods from terms defined for this study.

W1. Terminology, examples, and the meaning of trajectories

A warrant is the rule that licenses the target inference from premises PP to conclusion BB. The table clarifies the expressions raised in the review and identifies their locations in the submitted manuscript.

ExpressionMeaningOriginal locationRelation to cited work
Parent reasoning instanceOriginal problem and reasoning trace underlying the matched H/M/S variants.Introduction, p. 2; §3, p. 4; App. A.1.Our descriptive label for the matched construction.
Terminal validity marginValid final continuation's mean token log-probability minus the highest score among matched invalid alternatives.§3, Eqs. (10)–(11), pp. 5–6; App. B.2.Our metric; related to score-based patching evaluation, but distinct from the logit differences studied by Zhang & Nanda (2024).
Causal maturationChanges across layers in representation difference RℓR_\ell, decision alignment CℓC_\ell, and intervention effect FℓF_\ell, at a fixed checkpoint.Introduction, p. 2; §5.1, pp. 7–8; Fig. 3.Our descriptive term. We will clarify it as “layer-wise changes in causal influence.”
Finite causal leverageMeasured margin change after activation replacement; “finite” distinguishes the actual intervention from an infinitesimal derivative. FℓF_\ell averages both sign-aligned transfer directions.§3, Eq. (12); §5.1, Eq. (14); App. E.1.Activation patching is established; this name for FℓF_\ell is ours.
Productive parameter replacementCopying selected Healthy parameters into Severe increases the Terminal margin.§6, Eq. (20), p. 9; App. G.Sun et al. (2026) use parameter replacement; “productive” specifies our positive-gain criterion. Hase et al. (2023) distinguish localization from edit success.
Collateral reasoning benchmarks / metricsSecondary evaluations: Clean-NLL, ARC-Challenge, and RULER; not used to select intervention locations.§4; App. B.2 and C.4.Our umbrella label. We will consistently use “secondary evaluation metrics.”
TrajectoryAn optimization run in the training design; a layer-wise profile of Rℓ,Cℓ,FℓR_\ell,C_\ell,F_\ell in the depth analysis.Introduction; §5.1 and Fig. 3; App. B.1.Descriptive usage. We will explicitly distinguish training trajectories from layer-wise profiles.

We checked the relevant terminology in Zhang & Nanda (2024), Hase et al. (2023), and Sun et al. (2026). They provide methodological context, rather than definitions of our study-specific names.

Healthy, Mild, Severe, and “locally plausible.” In Figure 1A, PP is “Whales are mammals” and BB is “Whales are warm-blooded.” Only the warrant changes:

ConditionWarrant WWDoes BB follow from PP and WW?
HealthyAll mammals are warm-blooded.Yes
MildMost mammals are warm-blooded.No
SevereSome mammals are warm-blooded.No

“Locally plausible” means that Mild retains a broad generalization resembling the valid rule, but allows exceptions that could include whales. Severe weakens the warrant further: SOME requires only that warm-blooded mammals exist. Both corrupted warrants can be true while failing to justify BB. The severity labels describe the extent of corruption within the same operator family; they do not grade logical validity itself (§3; App. A.2).

W2. Definitions of the human-audit criteria

Appendix A.5 summarizes the checks but does not spell out each pass requirement. We will add the following rubric. Of 2,000 audited matched interventions, 1,952 passed all criteria (97.6%).

IDCriterionPass requirement
T1Parent IdentityH/M/S derive from the same original problem.
T2Target-edge ConsistencyAll target the same P+W→BP+W\rightarrow B dependency.
T3Operator FidelityMild and Severe use the same corruption family.
T4Mild InvalidityMild fails to license BB, despite local plausibility.
T5Severe InvaliditySevere clearly breaks the warrant's support for BB.
T6Severity OrderingSevere violates the same semantic dimension more strongly.
T7Alternative-route ExclusionNo valid route bypasses WW and still derives BB.
T8Non-target PreservationNo unrelated changes to P,B,D,CP,B,D,C or other non-target facts.
T9Semantic AlignmentAll variants retain the same reasoning task.
T10Confound ControlAvoid obvious group cues from length, style, or formatting.
AuthorsOpenReview ↗

Remaining Weaknesses, Questions, and Additional Findings

W3. Self-contained figures and numerical ranges

We will expand the captions.

  • Figure 1B: where activations transfer the H–S difference. 1C: layer-wise Rℓ,Cℓ,FℓR_\ell,C_\ell,F_\ell profiles. 1D: activation effects and successful weight replacements can occur at different layers.
  • Figure 2: A plots score margins; B plots their intervention-induced changes, both log-probability differences. Zero-based Later/Middle ranges (Table 11): Qwen-3B 23–35/12–18; Qwen-7B 18–27/9–14; Ministral 17–25/5–9; LLaMA 10–15/5–8. Captions will specify aggregation.
  • Figure 4: A1 tests held-out validity separation; A2 tests frozen layer-order predictions; A3 compares steering with an orthogonal control. Captions will define construction, splits, statistics, and strengths (α=−2,−1,0,1,2\alpha=-2,-1,0,1,2).

W4. Causal model, interventions, and assumptions

We distinguish interventions on training supervision, activations, and parameters. The training contrast τDWL=YH−YS\tau_{\mathrm{DWL}}=Y_H-Y_S holds the initial checkpoint, parent problems, optimization settings, and processed-token budget fixed. Here YY is the evaluation metric; interpretation assumes correct labels and matching.

Activation interventions fix the recipient's input and weights, replace selected states, and recompute the score. Transfer assumes comparable representation coordinates. Parameter replacement separately tests whether donor weights improve the recipient's score.

Disabled-patch and self-patch checks reproduce baseline outputs; same-condition cross-seed transfers measure generic transfer effects.

W5. Model sizes and training seeds

All four original models use three seeds (Table 6). We added Qwen3.5-2B/4B alongside Qwen2.5-3B/7B. Seed counts appear below. These test within-family replication, without claiming a monotonic scaling law.

Questions for Authors

No separate questions were listed; those embedded in the weaknesses are addressed above.

Additional findings: connecting the original analysis to generated proofs

All % changes denote absolute differences in rates.

1. The contrast extends to generated reasoning. We expanded training to 84,111 instances per condition: approximately 12.6M loss-bearing tokens for Qwen2.5-3B, 13.2M for Qwen3.5. On 1,200 provable ProofWriter questions, a symbolic checker verifies answer correctness and sufficient proof support. Models with positive mean H–S gains are:

ModelSeedsCorrect answer + sufficient proof: H–S
Qwen2.5-3B4+3.21%
LLaMA-3.2-1B3+4.28%
Ministral-3B4+2.92%
Qwen3.5-2B2+22.38%
Qwen3.5-4B1+12.33%

Means include all completed seeds per listed model. This complements candidate scoring.

2. Local reasoning and proof completion can move differently. On the controlled Qwen2.5-3B checkpoints (600 paired problems, three seeds), Healthy improves first-rule selection by 2.89%/4.33% on two-/three-step problems, but complete-proof accuracy changes by +9.17%/−7.33%. After supplying the correct first two steps, requiring one further rule choice reduces the three-step H–S third-rule gap from −22.56% to −0.50%. The model chooses among six rules; the correct rule is not supplied.

After that prefix, an L27 activation intervention moving Healthy toward Severe before generation reduces premature answering by 10.33% and improves three-step complete-proof accuracy by 5.17%, 95% CI [+4.00%, +6.44%]. The same intervention reduces two-step complete-proof accuracy by 7.50%, when the prefix already completes the proof. This identifies a continuation contribution.

3. Geometry explains the late-layer stopping effect. Let mstopm_{\mathrm{stop}} compare the log-probabilities of answering now and continuing with a rule. For fixed norm aa, the standard first-order relation is Δmstop,ℓ=aGstop,ℓCstop,ℓ+ϵℓ\Delta m_{\mathrm{stop},\ell}=aG_{\mathrm{stop},\ell}C_{\mathrm{stop},\ell}+\epsilon_\ell, where GG is gradient norm, CC directional alignment, and ϵ\epsilon the finite-intervention remainder. With Severe as recipient, the L27–L21 effect increases by 0.606 nats: alignment contributes +1.000, sensitivity −0.364, and the remainder −0.030. Thus stronger alignment, despite lower sensitivity, explains the larger effect here.

Intervals use paired problem bootstrap with training seeds fixed. These tests identify a stopping contribution, without estimating complete causal mediation.

DWL connects controlled differences in reasoning supervision to changes in internal causal organization and concrete generation decisions, showing that improved local reasoning does not necessarily translate into better complete proofs.

I thank the authors for their response. I appreciate the explanations for the terms above, still, I'd suggest revisiting whether the new terms are needed at all. As the writing is very difficult to follow, I will keep my score and encourage authors to rework teh paper and resubmit.

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

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