Does "Healing" a Damaged Language Model Restore Skill or Only Memorized Answers?

When a language model is damaged, whether by pruning weights, quantizing them to low precision, or deliberately removing knowledge, practitioners usually run a short "recovery" fine-tune. They then report that benchmark scores return close to where they were. Those benchmarks, though, are mostly public, and their questions have often leaked into training data. A recovered score could therefore mean two different things. The model may have rebuilt the ability to solve problems. Or it may simply be retrieving answers it had memorized, which survived the damage in fragments. This proposal measures how much of apparent recovery is the second kind. The method pairs each contaminated benchmark item with a freshly perturbed "twin" of equal difficulty, and plants contamination deliberately so we know exactly which items the model has seen.

The framing comes from peripheral nerve repair. There, surgeons reconnect a cut nerve and gross limb movement comes back, but fine, skilled movement does not. In a rat forearm model, large proximal muscles recovered ladder-walking performance, while intrinsic paw muscles showed no improvement over unrepaired controls, together with lasting muscle atrophy and cortical rewiring (Bao et al.). Conductive nerve conduits similarly regrow axons across a gap yet fail to restore toe extension (conductive conduits). Our hypothesis is that model recovery has the same two-speed structure. Memorized benchmark answers, which are cheap and redundantly stored, come back quickly, much like gross motor output. Procedural, compositional skill comes back slowly or not at all, like fine motor control. If static benchmarks are contaminated, they would measure mostly the fast component.

Core Claim

Recovery after damage to a language model is incomplete in a specific and measurable way. The fraction of lost accuracy that returns is systematically larger on items the model has memorized than on matched items it has not seen. Static contaminated benchmarks therefore overstate recovery. We further predict that the size of this gap depends on the shape of the damage.

This second prediction comes from an Active Inference simulation of stroke-like lesions (Simulating lesion-dependent functional recovery mechanisms). In that simulation, fully disconnecting one pathway let a backup pathway take over, and accuracy recovered to about 51%. Partial damage spread across both pathways left the system unable to decide which pathway to trust, and it stalled near 43%. Translated to networks, damage concentrated in whole layers ("focal") and damage spread thinly across all weights ("diffuse") could have the same immediate cost but different recovery trajectories.

We treat the biology as a source of testable predictions, not as evidence about language models. The claim stands or falls on the model experiments.

The quantity of interest is a recovery ratio computed separately for each class of item $c$:

$$R_c = \frac{A_c^{\text{rec}} - A_c^{\text{dmg}}}{A_c^{\text{int}} - A_c^{\text{dmg}}}$$

Here $A_c^{\text{int}}$, $A_c^{\text{dmg}}$ and $A_c^{\text{rec}}$ are the accuracies of the intact, damaged, and recovered model on item class $c$. We define contamination-inflated recovery as $R_{\text{orig}} - R_{\text{twin}}$, where "orig" means contaminated original items and "twin" means their perturbed counterparts. Normalizing by each class's own loss removes the objection that twins are simply harder. That objection is addressed a second time by building twins to match difficulty.

Research Program

The first component is controlled contamination. Relying on guesses about what a public model saw during training would be unreliable, so we plant contamination ourselves.

We start from an open base model in the 1–7B range. We continue its training on a general corpus into which label-level copies of a random half of several benchmarks are mixed. "Label-level" means questions together with their answers, which is the most severe tier in the contamination survey's taxonomy (Benchmark Data Contamination survey). The other half of each benchmark stays clean. The benchmarks are the MMLU test set (Measuring Massive Multitask Language Understanding), GSM8K and ARC-C. This design yields three item classes with known exposure: planted originals, clean originals, and twins of both.

The second component is the twins. Each MMLU, ARC-C and GSM8K item receives a Meta Probing Agents transformation, which paraphrases, restructures, or re-contextualizes the item while keeping its answer and content (MPA). The MPA authors report 94% equivalence and 97% correctness under human verification. We use the implementation in PromptBench.

We add two further item families whose difficulty we can control directly. The first is DyVal problems generated from directed acyclic graphs at complexity levels D1–D4 (DyVal). The second is random 3-SAT instances swept across the clause-to-variable ratio, including the hard region near 4.27 (3-SAT characterization). These families are the "fine motor" axis. They contain no memorizable answers, and their difficulty can be dialed up or down.

Following the "group scoring" idea from the Winograd study (Back to Square One), we also score each original–twin pair jointly: a pair counts as correct only if both members are answered correctly. That study showed group scoring cut a top model from 89.71% to 79.41% and exposed shortcuts that single-item scoring hid.

The third component is damage. We apply three kinds, each calibrated to produce the same drop on clean original MMLU items, so that comparisons are made at equal initial harm. Focal damage removes or zeroes a contiguous block of layers. Diffuse damage uses unstructured magnitude pruning or Gaussian weight noise across all layers. Targeted damage runs a standard unlearning method aimed at a subset of planted facts.

The last condition links to The Unlearning Mirage. That paper found unlearned knowledge still reachable at 20–30% accuracy through multi-hop queries. We ask the follow-up question it did not: after unlearning, does ordinary recovery training on unrelated data bring the "forgotten" answers back faster than it restores general skill?

The fourth component is recovery. We run recovery fine-tuning on a generic corpus that contains no benchmark text, and track learning curves at fixed checkpoints. Because the recovery data never contains the planted items, any return of accuracy on those items must come from residual memory the damage left behind. We record $R_c$ for every item class, damage type, and checkpoint.

Baselines

The naive reference point has two parts: the damaged model with no recovery, and the intact model. Together they fix the floor and ceiling of $R_c$.

The practice we are critiquing is recovery measured only on static original benchmarks. We run it exactly as a pruning or quantization paper would, and report its $R_{\text{orig}}$ as the "apparent recovery" number.

The strongest existing tool for separating memorization from skill is dynamic re-evaluation with MPA. On vanilla versus probed MMLU it reports a 15.7% accuracy drop for GPT-4-Turbo (MPA). We apply MPA to the intact, damaged, and recovered checkpoints with identical prompts, decoding settings, and judge model. The comparison with our design is fair because both use the same items and the same compute. Our method beats plain MPA re-evaluation if the planted-versus-clean contrast shows that the original-minus-twin gap in recovery is caused by contamination, rather than by paraphrase difficulty. Concretely, that means $R_{\text{orig}} - R_{\text{twin}}$ is significantly larger on planted items than on clean items, with clean items serving as the difficulty control.

For recovery methods themselves, no reported result was found on Lacuna for pruning or quantization recovery fine-tuning evaluated on dynamic benchmarks. We therefore establish that baseline ourselves, giving every recovery variant the same token budget and the same learning-rate sweep.

The ablation that isolates our key ingredient is to run the whole pipeline without planting, on a model with unknown natural contamination. If the conclusions do not change, controlled planting added nothing, and the cheaper observational design is enough.

Why not just…?

Why not just evaluate recovered models on a post-cutoff or private test set? This does give a clean number. It cannot say why that number differs from the static one, because a fresh test set changes content and difficulty along with exposure. The survey's Codeforces result shows exactly this pattern: GPT-4 declined on post-cutoff problems, but a time split cannot tell a memorization loss from a harder problem distribution (survey). Our planted/clean split holds content fixed and varies only exposure. The clean-item $R_{\text{twin}}$ in our design is essentially this baseline, so the comparison is built in.

Why not just run a membership-inference or n-gram overlap detector on the recovered model? Detectors estimate whether an item was seen. They do not estimate how much of the recovered accuracy depends on having seen it. An item can be detectably memorized and still be solved by genuine skill. We will run a loss-based membership score as a covariate and test whether it predicts per-item recovery. If it predicts recovery as well as the twin gap does, that is a real threat to the value of twins, and we will report it as such. We found no reported result on Lacuna for detector-based analysis of recovery.

Why not just assume more recovery data or a larger model closes the gap? This is a genuine alternative, and we test it rather than dismiss it. We sweep recovery tokens across an order of magnitude and run the pipeline at two model sizes. Prior evidence makes a full close unlikely for procedural items. GPT-4 fell to about 10% on 3-SAT search at the phase transition (3-SAT). Models strong on static math scored near zero on DyVal (DyVal). If $R_{\text{twin}}$ converges to $R_{\text{orig}}$ with enough recovery data, the correct conclusion is that the gap is a transient speed difference, not permanent incompleteness. That would still be useful, because it would tell practitioners how long to heal before trusting static scores.

Proposed Experiments

The decisive first check uses diffuse damage calibrated to a matched MMLU drop. The prediction is that $R_{\text{orig}}$ on planted items exceeds $R_{\text{twin}}$ by a clear margin, while the same difference on clean items stays near zero. If the planted and clean gaps are equal, contamination is not the explanation and the core claim fails.

The second check tests the lesion-shape prediction taken from the Active Inference model. At equal initial damage, the prediction is that diffuse damage yields lower final $R_{\text{twin}}$ than focal damage, and that the difference grows with DyVal level and near the 3-SAT hard region. We expect the difference to be small or absent on memorized items. Observing the opposite ordering would falsify the analogy and be reported as such.

The third check covers targeted damage. We track how fast planted answers resurface during generic recovery, compared with how fast skill returns on twins, and measure resurfacing with both single-hop and multi-hop probes in the style of the Unlearning Mirage. The question is whether recovery training quietly undoes unlearning, which matters for anyone who unlearns a model and then keeps fine-tuning it.

Across all checks we report per-class recovery curves with bootstrap confidence intervals over items and three random seeds. We also report the group-scored pair accuracy, which gives the single most interpretable number: the fraction of original–twin pairs the recovered model gets right together.