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The Fragility of Reasoning-Importance Attribution for Pruning Language Models

Abstract

Attribution-guided pruning scores components by their causal contribution and protects the important ones, and it is increasingly applied to compress reasoning language models without destroying their chain of thought. Its reliability rests on an unexamined assumption: that reasoning importance can be faithfully measured. Across four small reasoning models, we show this measurement is fragile in three ways, each of which changes pruning decisions. First, scoring final-answer tokens, the natural choice, saturates in every chain-of-thought model we test (answer-token negative log-likelihood, NLL, of 10−410^{-4}–10−310^{-3}) because the model states its answer inside its own reasoning; guiding head pruning with this target costs 27.6 and 32.2 accuracy points relative to scoring reasoning tokens on the two models we power with five seeds, while perplexity barely moves and even reverses sign at 7B. Second, causal importance is not localizable to single units: single-neuron effects sit at the measurement floor, their cross-split ranking is noise, and they cancel: a group's ablation effect disagrees in sign with the summed effects of its members in 90% of groups. Reproducible importance emerges only at groups of ∼100\sim 100 neurons. Third, contrastively isolated ``reasoning-specific'' importance is not separable from generic importance, and protecting it is worse than protecting raw importance. We additionally pre-registered the hypothesis that distillation-induced concentration of importance predicts the pruning cost; it is not supported, and since our grid confounds concentration with scale, we report it as unresolved rather than reversed. The result is a short set of measurement rules: score reasoning tokens, attribute at coarse granularity, and evaluate with accuracy rather than perplexity.

Introduction

Small language models with chain-of-thought (CoT) reasoning ((Wei et al., 2022)) are attractive targets for on-device deployment, and pruning is the standard route to shrink them. Classical pruning scores parameters by their contribution to language-modeling loss ([5, 4, 11]), and a recent line of work makes pruning reasoning-aware: calibrating on self-generated CoT activations ([6]) or attributing importance causally and protecting high-scoring components ((Sheth et al., 2025)), echoing interpretability findings that specific heads carry outsized functional load ([8] (Voita et al. 2019)).

All such methods share an unexamined dependency: they assume the reasoning-importance signal is faithful. Attribution requires three implicit choices: what to score against (the target token set), at what granularity to score, and whether reasoning-specific components are separable from generally important ones. We show each choice is fragile in reasoning models, and that the first has large, measurable consequences for pruning.

Our thesis is restatable in one sentence: to guide pruning without silently degrading reasoning, importance must be scored on reasoning tokens rather than answer tokens, measured over groups of at least ∼ 100 units rather than single components, and taken as raw importance rather than a reasoning-specific contrast. We frame this as a methodological complement to reasoning-aware pruning, not a critique of any method. We verified from source that the two closest methods do not use the saturating target: the reconstruction-based pruner of Lucas et al. [6] reconstructs weights over prompt and decode tokens, which include the chain of thought, and the causal-attribution pruner of Sheth et al. [10] scores a span that is not the model’s own CoT followed by its answer, and is evaluated on non-distilled instruct models. The saturating target is a naive-but-plausible choice that we characterize, not a flaw we attribute to prior work.

Contributions.

  • Target fragility. Final-answer-token attribution saturates in all four models (§ 4) and, used for head pruning, costs +27.6 (D1) and +32.2 (N1) accuracy points versus scoring CoT tokens, with tight hierarchical-bootstrap intervals over five seeds (§ 5).

  • Granularity fragility. Single-neuron causal importance is ill-posed: effects are irreproducible and cancel (sign disagreement 0.90); reproducible importance emerges only at G∗≈100G^\ast\approx100 (§ 7).

  • Specificity fragility. Reasoning-specific importance collapses to its own noise floor, and protecting the specific set is worse than protecting the generic set at every budget (§ 8).

  • A pre-registered negative. The hypothesis that concentration explains the pruning cost is tested and unsupported; we report it as unresolved, not reversed (§ 6).

  • Accuracy–perplexity decoupling. The damage is visible in accuracy but not perplexity; at 7B the two endpoints disagree in sign (§ 5).

Related Work

Reasoning-aware pruning. Reconstruction-based (Frantar & Alistarh [4]) and activation-magnitude (Sun et al. [11]) pruning are reasoning-blind. Recent methods inject self-generated CoT into calibration (Lucas et al. [6]) or score components by causal contribution and protect the important ones (Sheth et al. [10]). Structured pruning of whole units, including attention heads, has a long history (Michel et al. [8]; Voita et al. (2019); Ma et al. [7]). We do not propose a new mask; we audit the reliability of the importance signal these methods consume, which is complementary and, we argue, prior.

Causal attribution and circuit localization. Our estimators follow the activation-patching tradition (Conmy et al. [2]) and its gradient approximation, attribution patching (Syed et al. (2023)), whose known failure modes at fine granularity our granularity result quantifies in the reasoning setting. Interpretability work reports that specific heads carry disproportionate functional load (Michel et al. [8]; Voita et al. (2019)); we ask whether such localization transfers into a reliable pruning prior, and find specific limits.

Setup

Models. We use a 2×22 \times2 grid over distillation and scale: two reasoning-distilled models, DeepSeek-R1-Distill-Qwen-1.5B (D1) and -7B (D2) (DeepSeek-AI et al. [3]), and two size/family-matched non-distilled instruct models, Qwen2.5-1.5B-Instruct (N1) and Qwen2.5-7B-Instruct (N2) (Qwen Team [9]). D1/D2 are distilled from the Qwen2.5 family, making N1/N2 near-matched controls.

Scoring targets. We measure the importance of a component by how much removing it raises the model’s loss on a chosen set of tokens. Concretely, head importance is the increase in negative log-likelihood (NLL) on that token set when a query head’s output is mean-ablated, that is, replaced by its average over the calibration set (a standard way to delete a component’s contribution while keeping activation statistics in range). The scoring target is precisely this set of tokens: the choice of which tokens to score is the free decision that attribution methods must make, and it is our object of study. We compare three targets: TansT_{\mathrm{ans}} = final-answer tokens with the CoT present (the naive choice); TcotT_{\mathrm{cot}} = the CoT reasoning tokens (the corrected choice); and TrecT_{\mathrm{rec}} = answer tokens with the CoT removed, a control isolating whether the pathology is answer tokens per se or answer-after-CoT.

Pruning and evaluation. We prune at the granularity of whole query heads for three reasons. First, the attribution-guided methods we audit operate on heads and comparable coarse units, so this is where a reasoning-importance ranking actually drives a pruning mask. Second, a head is structured hardware-friendly compute (an entire attention sub-computation), unlike an individual weight. Third, our own granularity result (§ 7) shows that importance is not reliably measurable at the level of single neurons, so the head is close to the finest unit at which the ranking is trustworthy. Concretely, we prune a query head by zeroing the corresponding rows of the query projection WQW_Q and columns of the output projection WOW_O; under grouped-query attention the key and value projections are shared across heads and we leave them untouched (we assert a maximum ∥WK∥,∥WV∥\lVert W_K\rVert,\lVert W_V\rVert norm change of exactly 0.0 for every model). We report accuracy (exact match, permissive extractor accepting \boxed{}, “the answer is X”, or the final number), CoT-token NLL, and format-success rate on ≥500\ge500 held-out problems from GSM8K, a grade-school math word-problem benchmark [1]; calibration is drawn from the training split, so held-out evaluation is disjoint by construction. To compare models at matched operating points we sweep the pruned-head fraction and use each model’s f1/2f_{1/2}, the fraction at which accuracy reaches half of dense, requiring that the swept curve contains a point in the 25–50%-of-dense band (all four models pass; no gap is computed on a floored curve). Calibration uses 128 correctly-answered CoT trajectories per seed; each seed resamples calibration, recomputes importance, re-prunes, and re-evaluates. We run five seeds at 1.5B and three at 7B; all intervals are hierarchical bootstraps resampling both seeds and test items, and we report seed standard deviations rather than item-only pp-values on seed-averaged accuracy.

Compute and implementation. Every experiment runs on a single NVIDIA H100 (80GB); no result requires multi-GPU execution, and the full set of jobs totals roughly 75 GPU-hours. Models are loaded in bfloat16 and decoded greedily with a 1024-token budget, so the only stochasticity in our pipeline is the calibration draw. We use PyTorch 2.13 and Transformers 5.13; exact versions ship with the code release.

Operating points and the accuracy cliff. Reasoning accuracy under head pruning does not decay smoothly: it holds near dense and then falls sharply, which makes any single sparsity level a poor basis for comparison and can confound a measurement entirely. We therefore locate each model’s operating point empirically (Table 1) and require, as a pre-registered gate, that the swept curve contain a point between 25% and 50% of dense accuracy; only then is a gap computed on that curve. For the 1.5B models the cliff is steep enough that a coarse sweep skipped the band and the gate correctly rejected it; refining to single-head steps recovered a genuine slope. All four models pass with accuracy as the primary endpoint, so no result in this paper is read off a floored curve. Reported variance is over calibration resampling, which we find dominates: it is the seed standard deviation, not test-item noise, that sets the width of our intervals.

ModelTotal headsDense acc.f1/2f_{1/2} (heads)f1/2f_{1/2} (%)Range-check
D133662.7%4011.9%pass
N133670.7%4413.1%pass
D278465.3%11815.1%pass
N278493.3%11815.1%pass

Table 1. Per-model operating points from the locating sweep (150 held-out items, one seed). f1/2f_{1/2} is the pruned-head count at which accuracy reaches half of dense. All four pass the range-check gate, so accuracy is the primary endpoint throughout.

Answer-Token Attribution Saturates Universally

The default scoring target is degenerate in every model we test. With the CoT in context, the answer-token NLL is 9×10−59 \times10^{-5} to 3.6×10−33.6 \times10^{-3} (Table 2): a CoT ends by stating its answer, so re-predicting that answer is near-trivial and the target carries almost no signal. What little signal remains is highly concentrated: in the distilled models one head out of hundreds holds ≥0.96\ge0.96 of the total importance mass.

ModelDistilledTansT_{\mathrm{ans}} NLLLeakage (Trec−TansT_{\mathrm{rec}}-T_{\mathrm{ans}})TansT_{\mathrm{ans}} GiniTansT_{\mathrm{ans}} top-1 mass
D1 (R1-Distill-Qwen-1.5B)Y0.000651.6510.9870.969
N1 (Qwen2.5-1.5B-Instruct)N0.000201.5400.9160.260
D2 (R1-Distill-Qwen-7B)Y0.000091.4560.9970.996
N2 (Qwen2.5-7B-Instruct)N0.003621.2440.8430.598

Table 2. Answer-token attribution (TansT_{\mathrm{ans}}) saturates in all four models. Leakage (Trec−TansT_{\mathrm{rec}}-T_{\mathrm{ans}}) is universal and is not larger in the distilled models; concentration of the saturated signal is.

What causes this saturation is answer-in-CoT leakage: a chain of thought typically states the final answer within the reasoning text before the designated answer span, so once the CoT is in context the answer tokens are nearly deterministic and carry little residual loss. We can measure the strength of this leakage as the rise in answer-token NLL when the CoT is removed from context (Trec−TansT_{\mathrm{rec}}-T_{\mathrm{ans}}): a large rise means the answer was hard to predict without the CoT and easy with it. This leakage is universal rather than distillation-specific. The rise is large in all four models (1.24–1.65) and is in fact larger in the non-distilled model N1 (1.54) than in the distilled model D2 (1.46), so it is a property of step-by-step-then-answer generation itself, not of distillation. What does track distillation is how concentrated the resulting saturated signal becomes (Table 2, last column), which we examine in § 6. Across all models TansT_{\mathrm{ans}} ranks heads nearly orthogonally to TrecT_{\mathrm{rec}} (Spearman −0.008 to 0.119) and only weakly agrees with TcotT_{\mathrm{cot}} (0.120–0.347), so TansT_{\mathrm{ans}} is anomalous relative to both other targets. The pathology is the answer-after-CoT copy effect, not answer tokens broadly.

The Saturating Target Misguides Pruning

Saturation would be harmless if it did not change decisions; it does. Pruning by TansT_{\mathrm{ans}} rather than TcotT_{\mathrm{cot}} importance at each model’s f1/2f_{1/2} costs 27.6 accuracy points on D1 (95% CI [+18.8, +37.3], p<0.001p < 0.001) and 32.2 on N1 (CI [+26.4, +38.6], p<0.001p < 0.001), positive in all five seeds of both models (Figure 1, Table 3). The mechanism is visible in the masks: because the saturated ranking assigns almost all mass to one head, it protects that head and orders the rest near-arbitrarily, so accuracy collapses to near-chance and format-success falls to 56–64%. The corrected target holds format-success above 97% at the same sparsity. The TrecT_{\mathrm{rec}} control reproduces the effect (Δ(Tcot−Trec)=+27.6\Delta(T_{\mathrm{cot}}-T_{\mathrm{rec}}) = +27.6 on D1, +35.9 on N1), so the benefit comes from scoring reasoning tokens rather than from any peculiarity of the answer span.

Figure 1. The saturating target’s pruning cost. Bars are Δ=acc⁡(Tcot)−acc⁡(Tans)\Delta= \operatorname{acc}(T_{\mathrm{cot}}) - \operatorname{acc}(T_{\mathrm{ans}}) at each model’s own f1/2f_{1/2}, with hierarchical-bootstrap 95% intervals and per-seed values overlaid. The two five-seed 1.5B models (blue) show a large cost that is positive in every seed; the three-seed 7B models (grey) are underpowered and we do not draw conclusions from them.

ModelSeedsDensef1/2f_{1/2}Δ\Delta (points)seed s.d.95% CIpp
D1563.0%40+27.610.4[+18.8, +37.3]< 0.001
N1574.0%44+32.25.9[+26.4, +38.6]< 0.001
D2371.2%118−1.1 (unres.)17.5[−18.6, +21.2]0.79
N2391.2%118+20.520.5[−7.4, +38.4]0.07

Table 3. Pruning by the saturating target (TansT_{\mathrm{ans}}) versus the corrected target (TcotT_{\mathrm{cot}}) at each model’s own f1/2f_{1/2} (in heads). Δ>0\Delta> 0 means the saturating target costs accuracy. The seed standard deviation makes the power difference explicit: it is 5.9–10.4 points on the five-seed 1.5B models but 17.5–20.5 on the three-seed 7B models, which is why we label D2 unresolved rather than null. Intervals are hierarchical bootstraps over seeds and test items.

The 7B results point the same way but are underpowered at three seeds: N2 shows +20.5 (CI [−7.4, +38.4], p=0.07p = 0.07) and D2 shows −1.1 (CI [−18.6, +21.2], p=0.79p = 0.79) with per-seed values that flip sign (−7.2, +22.8, −18.8). We therefore treat D2 as unresolved, not as a null: three seeds cannot resolve an effect of this variance. The robust, well-powered conclusion is at 1.5B: the naive answer-token target imposes a large reasoning-accuracy cost, and importance should be scored on reasoning tokens.

Accuracy–perplexity decoupling. The damage is not faithfully reflected in perplexity. On D1, TansT_{\mathrm{ans}}-guided pruning inflates CoT-NLL by +3.18 alongside the accuracy collapse; but on D2 and N2 the NLL gap is negative (−0.20, −0.35) even where the accuracy gap is positive. The two endpoints disagree in sign at 7B. Perplexity-only evaluation of pruned reasoners can therefore understate or misrank the damage, a caution that applies to any compression work reporting perplexity alone.

The gain is not recoverable from a reasoning-blind score. A natural objection is that the corrected target merely recovers what a standard magnitude criterion would give. It does not. We include a target-agnostic weight-magnitude baseline (the sum of WQW_Q-row and WOW_O-column norms per head) at every operating point (Figure 2, ×): at f1/2f_{1/2} it sits at or near the floor in all four models, for example 1.2% and 0.8% accuracy on D1 at 40 and 44 heads. The signal that TcotT_{\mathrm{cot}} supplies is therefore not a proxy for weight magnitude. We also emphasise that we do not propose a mask: our object of study is the importance signal that a mask consumes, and our recommendations apply to any method that consumes one.

Figure 2. Accuracy versus pruned heads under the corrected target TcotT_{\mathrm{cot}} (green), with TansT_{\mathrm{ans}} (▼), the TrecT_{\mathrm{rec}} control (■) and a target-agnostic weight-magnitude baseline (×) evaluated at each model’s f1/2f_{1/2} (orange dashed line); markers are offset horizontally so they remain distinguishable where they coincide near the floor. The grey line and right-hand axis give format-success rate, which stays high along the TcotT_{\mathrm{cot}} sweep, so the decline is loss of reasoning rather than loss of output structure. The magnitude baseline sits at or near the floor at f1/2f_{1/2} in all four models, so the TcotT_{\mathrm{cot}} advantage is not recoverable from a reasoning-blind score.

Concentration Does Not Explain the Pruning Cost

§ 4 and § 5 established two facts about the saturating target: its importance mass concentrates onto a single head, and pruning with it is costly. Before the pre-registration we conjectured that the first explains the second, and we report the test of that conjecture here.

Concentration tracks distillation sharply (Table 2): the TansT_{\mathrm{ans}} top-1 head holds 0.969/0.996 of the mass in D1/D2 versus 0.260/0.598 in N1/N2. A robustness diagnostic indicates this is structural rather than an artifact of near-zero scores: in the distilled models the dominant head is identical across all five calibration resamples and decisive over the runner-up (113× for D1, 6539× for D2), and it coincides with the top head under the corrected target TcotT_{\mathrm{cot}}; in non-distilled models it is unstable across resamples (N1, two distinct winners) or far less decisive (N2, 16×). D1 and D2 concentrate onto the same head position across a 4.6× scale gap.

We pre-registered the prediction that this concentration explains the pruning cost: if TansT_{\mathrm{ans}} collapses onto one head, TansT_{\mathrm{ans}}-guided pruning protects one head and prunes the rest near-randomly, so more concentrated models should show larger gaps. The prediction is not supported. Across the four models the rank correlation between concentration and Δ\Delta is −0.80, if anything inverse: the most concentrated model (D2, 0.996) shows the smallest, non-significant gap and the least concentrated (N1, 0.260) the largest. Two facts prevent us from claiming a genuine inverse effect. The correlation rests on four points, two of which (D2, N2) are noise-dominated at three seeds; and concentration is confounded with scale in this grid, since both high-concentration models are the 7B ones, so the trend may reflect “7B is more robust to head pruning” rather than anything about concentration. We therefore report the concentration mechanism as tested and unresolved, and defer a de-confounded test (concentration varied within a fixed scale, with a powered 7B arm) to future work.

We report this negative in full because it is the honest outcome of a pre-registered prediction; we draw no mechanism claim from it, and none of our recommendations depend on it.

Reasoning Importance Is Not Finely Localizable

The target choice was the first of the three attribution decisions from § 1; we now turn to the second, the granularity at which importance is scored. Here the fragility is not that a plausible choice misfires but that the finest choice is ill-posed: causal reasoning-importance is not measurable at single-unit granularity. Ablating groups of GG MLP neurons (individual feed-forward hidden units, the post-SwiGLU activations feeding down_proj; 8,960 per layer and 250,880 in total for D1) and measuring the effect on CoT-token NLL, single-neuron effects sit at the measurement floor (2.4×10−52.4 \times10^{-5} median, against a floor of 1.0×10−41.0 \times10^{-4} estimated from a rounding-scale sham perturbation).

Figure 3. The pre-registered concentration mechanism, shown for completeness and not as a result. Each point is one model (n=4n = 4); grey squares are the underpowered three-seed 7B models. With four points, two of them noise-dominated, and concentration confounded with scale, this panel cannot support either a positive or an inverse mechanism claim.

and their cross-split ranking is noise. Here split-half Spearman denotes the rank agreement between importance scores computed on two disjoint halves of the calibration set, where 1 is perfect agreement and 0 is chance; for single neurons it is 0.059 at G=1G=1 and −0.366-0.366 at G=3G=3. Reproducible importance emerges only near G≈100G \approx100: split-half Spearman rises from 0.367 at G=30G=30 to 0.781 at G=100G=100 and stabilises above 0.8 thereafter (Figure 4b). Two independent criteria, the reproducibility onset and the numerical-floor crossing, both place G∗G^* at 100.

Figure 4. Reasoning importance is not localizable below ∼100 neurons. (a) Median ∣ΔNLL∣|\Delta\mathrm{NLL}| from ablating GG neurons grows with GG; single neurons sit at the measurement floor (dashed line, estimated from a rounding-scale sham perturbation). (b) Split-half Spearman between independent calibration halves crosses the 0.7 bar only at G∗=100G^{*}=100 (green dotted line in both panels). (c) Cancellation: each point is one 100-neuron group, plotting the group’s measured ΔNLL\Delta\mathrm{NLL} against the signed sum of its members’ individual effects (both axes in units of 10−310^{-3}). The summed singletons are negative for all 50 groups while the group effect is positive for 45 of them, so single-unit effects do not compose.

The mechanism is cancellation, not mere redundancy. Across 50 groups of 100 neurons, the group’s ablation effect is positive in 90% of cases while the signed sum of its members’ individual effects is negative in all 50, a sign disagreement of 0.90 (Figure 4c), with the group effect a median 0.105×0.105\times the magnitude of the summed singletons. Individual neuron effects do not compose; they cancel. Single-neuron causal attribution, sometimes proposed as a finer-grained refinement of head-level methods, is therefore numerically ill-posed at this scale, independent of estimator: the quantity being estimated is itself below the floor.

Reconciling with head-level sensitivity. This may appear to contradict the finding that individual heads matter a great deal (§ 5, and the appendix probe). It does not. A head is a large routing object, 128 dimensions writing to the residual stream through WOW_{\mathrm{O}}, whereas an MLP neuron is one of 8,960 per layer. Redundancy and cancellation operate at the sub-unit scale; heads are already coarse enough to be individually measurable. Our result is a statement about where the measurement floor sits, and it places that floor between the neuron and the head.

Reasoning-Specific Importance Is Not Separable

The third attribution decision is whether reasoning-specific components can be isolated from generically important ones, as circuit-localization work suggests and as a protection scheme might exploit. Contrastively isolated “reasoning-specific” importance, defined as reasoning contribution minus a matched non-reasoning baseline, is not separable from raw importance for masking. At head level the reasoning-specific contrast collapses to its own split-half noise floor: the divergence between the specific ranking and raw importance is 1.00, 1.08 and 0.97 times that floor at k=5k = 5, 10 and 20%. That is, the specific ranking disagrees with raw importance no more than it disagrees with itself across data splits. Introducing a length- and token-type-matched control (shuffled-CoT, itself highly reproducible at split-half Spearman 0.983) shrinks the apparent divergence further: the rank correlation with raw importance rises to 0.509 and the top-kk overlap ratio (0.71–0.79) fails a pre-set separation bar of 0.7.

At neuron level the decision-relevant test is direct: ablating the top reasoning-specific group is less damaging to reasoning than ablating the top raw-importance group at every budget (ΔNLL\Delta\mathrm{NLL} 0.42 vs 0.70 at 1%, 0.98 vs 1.31 at 5%, 1.47 vs 1.68 at 10%; random groups 0.007–0.085). Protecting the “specific” set is thus worse than protecting the generically important set. Reasoning-specific components, insofar as they can be measured at all, are largely the generically important components.

Discussion and Recommendations

The three fragilities yield concrete guidance for attributing reasoning-importance in CoT models, for pruning and equally for analysis or data selection.

  • Score reasoning tokens, not answer tokens. Answer-token targets saturate in every CoT model tested and, for pruning, cost 27–32 accuracy points at 1.5B. Score the CoT span.

  • Do not attribute at single-unit granularity. Neuron-level causal importance cancels and is irreproducible; use groups of ≳100\gtrsim100 units, or coarser objects such as heads.

  • Do not rely on reasoning-specific localization. Specific and generic importance are not separable for masking; contrastive protection does not beat raw importance.

  • Evaluate with accuracy, not perplexity. The two decouple under reasoning pruning and disagree in sign at 7B.

Each is inexpensive to apply, and they complement rather than replace existing reasoning-aware pruning methods.

Scope of the claims. We are explicit about what each finding is powered to support. The universal saturation of TansT_{\mathrm{ans}} (§ 4) is measured in all four models and is the broadest claim. The pruning cost (§ 5) is established at 1.5B with five seeds on GSM8K, and we deliberately do not generalise it to 7B or to other tasks; the 7B arm is reported so that a reader can see its variance rather than omitted because it is inconvenient. The granularity and specificity results (§ 7 and § 8) are measured on one model family and we present them as such. The concentration mechanism is unresolved. We would rather state a narrow claim that holds than a broad one that does not.

Limitations

Our well-powered evidence is at 1.5B on GSM8K with five seeds; the 7B arm has three seeds, does not resolve the concentration hypothesis, and leaves D2’s gap indeterminate. Concentration is confounded with scale in our 2×22 \times2 grid, so § 6 cannot separate the two. We study attention-head pruning; head-level protection is in tension with the 2:4 semi-structured sparsity formats (two nonzero weights per group of four, which GPUs accelerate) that deliver kernel speedups, and we do not report end-to-end latency, so our claims are about the signal, not about achieved compression. Our estimators are mean-ablation for heads and attribution patching for neurons; the latter did not pass a per-neuron validation gate (rank-stratified Spearman 0.65 against true ablation), which is why we report neuron results only at the collective, group level, and which is itself consistent with the granularity finding. Task coverage is math reasoning; extending to non-math CoT is future work. The single-head probe in Appendix § 12 is preliminary and uncontrolled, and we draw no claim from it.

Conclusion

Attribution-guided pruning of reasoning models rests on an importance signal that is fragile to measure. The natural answer-token target saturates in every CoT model and, used for pruning, collapses reasoning accuracy while barely moving perplexity; causal importance is not localizable below ∼100\sim100 neurons because single-unit effects cancel; and reasoning-specific importance is not separable from generic importance. A pre-registered concentration mechanism is tested and unresolved. The practical consequence is a set of measurement rules that make reasoning-importance attribution reliable, offered as a complement to the reasoning-aware pruning literature.

Preliminary single-head ablation (not controlled; no claim drawn)

As a preliminary probe of the concentrated head’s causal role, ablating that single head alone reduced GSM8K accuracy from 60.4% to 2.6% on D1 and from 68.8% to 1.4% on D2 (its own dense decode; 500 held-out items). Ablating a random early-layer head instead cost −0.6 points on average on D1 (three draws: −0.4, +3.2, −4.6).

We draw no conclusion from this. The random baseline is three draws, not a distribution; on D2 the three random early-layer draws were +1.2, −1.8 and +45.4 points of damage (mean +14.9), i.e. one randomly chosen early-layer head was itself worth 45 points, so at 7B the target head is not cleanly separable from other early-layer heads. We have also not disentangled reasoning degradation from generation/format collapse. A controlled version, ablating the target head against a distribution of 10 to 20 random heads per layer band, with format-success reported and a matched-capacity control, is required before any single-head causal claim, and is left to future work.

Reproducibility

We report all seeds, calibration draws, held-out test identifiers and per-job artifact hashes with the code release. The code, data-processing scripts, and figure-generation scripts are available at https://github.com/himans-iitk/Reasoning_in_Pruning. Pruning is deterministic given an importance vector; reported variance is over calibration resampling (five seeds at 1.5B, three at 7B). Intervals are hierarchical bootstraps over seeds and test items. Key-value projections are verified unchanged under head pruning (maximum norm delta 0.0 in all four models).

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