{"id":"5b4b6b50-c7ee-421b-809d-acd731aaeb93","arxiv_id":"2607.05271","paper_version":1,"verdict":"CONDITIONAL","confidence":"MODERATE","novelty_score":6.0,"correctness_risk":"unknown","formal_verification":"none","parameter_count":12,"one_line_summary":"TGSR-PINN improves PINN inverse-problem transfer learning by scoring neuron relevance to the target task via Taylor sensitivity and pre-activation variance, then applying continuous soft decay to low-scoring neurons rather than hard pruning or random resetting.","lead":"This paper proposes a method (TGSR-PINN) that improves how physics-informed neural networks recover physical parameters when transferring knowledge between different PDE inverse problems. It identifies which neurons in a transferred network are unhelpful for the target task and gently reduces their influence, improving parameter recovery accuracy without destroying useful learned representations.","discovery_kind":"unclear","skeptic_critique":{"model":"glm-5.2","headline":"Main-experiment baseline comparisons lack pairwise statistical tests; effect sizes vs. Lightweight FT are within one standard deviation, so the headline improvement over baselines is not statistically established.","rationale":"The reader correctly identified the large standard deviation and cherry-picking of the best repetition as evidence-quality issues, and the short-adaptation contamination concern is a legitimate mechanism-level vulnerability. However, the most load-bearing issue is more fundamental: the main-experiment comparisons against actual baselines lack any reported significance tests, and the effect sizes—particularly vs. Lightweight FT—are small relative to the standard deviations. The counterfactual ablations, while well-designed and statistically tested, only prove that the scoring mechanism is better than random perturbation, not that the full method significantly outperforms the best existing baseline. This distinction matters because the headline claim explicitly states improvement over 'full fine-tuning, lightweight fine-tuning, and other baselines.' The paper's paired comparison protocol (§3.1) suggests the data to run these tests already exists; reporting them would either confirm or weaken the headline claim at low cost. The verdict remains CONDITIONAL because the method is well-motivated, the counterfactual ablations are convincing for the mechanism question, and the code is public—but the baseline-comparison evidence needs statistical verification before the central claim can be fully accepted. If the pairwise tests turn out non-significant for the key baseline comparisons, the claim should be narrowed from 'improves over baselines' to 'provides a mechanism that reduces perturbation relative to random alternatives, with comparable performance to the best baseline.'","tokens_in":24771,"tokens_out":2978,"duration_ms":31760,"concrete_test":"Run paired Wilcoxon signed-rank tests between TGSR-PINN and each baseline (Full FT, Lightweight FT, Partial Transfer, TL-gPINN, BitFit) on the existing 7-repetition high-Péclet data and 11-repetition Allen–Cahn→Burgers data, using the paired comparison protocol described in §3.1. If TGSR-PINN vs. Lightweight FT in the high-Péclet task yields p>0.05 (which is likely given the 0.4 pp mean difference and SDs of ~2.4–3.0%), the claim of improvement over baselines should be narrowed to 'improvement over Full FT' or qualified as a trend rather than an established advantage.","verdict_should_be":"CONDITIONAL","load_bearing_attack":"The central claim that TGSR-PINN improves parameter recovery over baselines rests on Tables 3 and 5, which report means and standard deviations but no pairwise significance tests. In the high-Péclet task (Table 3, n=7), TGSR-PINN's average parameter error of 4.426±3.019% vs. Lightweight FT's 4.825±2.384% is a 0.4 percentage-point difference—well within one standard deviation of either method. The α-specific mean error is ~13.25% (per §3.5.3), and the prominently featured 0.38% best-α result (Table 4) is selected from 7 repetitions. In the Allen–Cahn→Burgers task (Table 5, n=11), TGSR-PINN's ν error of 0.408±0.260% vs. Full FT's 0.568±0.399% is a 0.16 pp difference with overlapping standard deviations. The counterfactual ablations (Table 8, n=10) do report Wilcoxon tests (p=0.037, p=0.014), but these compare TGSR-PINN against degraded versions of itself (Random Soft Decay, Score-Shuffled), not against the actual baselines. This means the evidence supports 'the scoring mechanism matters relative to perturbation' but does not establish 'TGSR-PINN significantly outperforms the best baseline.' The paper states it uses a paired comparison protocol (§3.1), so paired data likely exists, but the tests are not reported. Without them, the headline claim of improvement over baselines—especially over Lightweight FT—remains statistically unverified.","agreement_with_reader":"partial"},"referee_report":{"model":"glm-5.2","summary":"The paper proposes TGSR-PINN, a neuron-level representation correction method for PINN inverse transfer learning. After transferring only network weights/biases from a source model (not physical parameters), the method performs a short target-adaptation phase, computes neuron target scores using first-order Taylor sensitivity and pre-activation variance, estimates weak-adaptation signals via a GMM with rank fallback, and applies selective soft decay to low-scoring neurons under layer protection. The method is evaluated on three tasks: high-Péclet 2D advection-diffusion, Allen-Cahn→Burgers cross-PDE transfer, and 5%-noise reaction-diffusion. Ablation studies examine scoring components, GMM/rank fallback, layer protection, and decay mapping forms. The central claim is that target-evidence-driven neuron scoring and selective soft decay improve physical parameter recovery compared to standard fine-tuning baselines, while maintaining comparable field accuracy.","tokens_in":25619,"tokens_out":1700,"duration_ms":70495,"significance":"The paper addresses a genuine problem: in PINN inverse transfer learning, field accuracy and parameter recovery can decouple, and coarse-grained transfer strategies may not address neuron-level representation mismatch. The methodological pipeline is well-motivated and internally consistent. Strengths include: (1) counterfactual ablations (Table 8) with Wilcoxon tests (p≤0.037) demonstrating that the benefit is not from arbitrary perturbation; (2) layer protection ablation (Table 14, p=0.002) and decay mapping ablation (Table 15, p≤0.004) with 10 paired repetitions; (3) public code availability at a GitHub repository; (4) honest discussion of applicability boundaries, including acknowledgment that the GMM branch is not the primary active route in the high-Péclet task (§3.5.4). The paper is transparent about the large standard deviations in the high-Péclet task and positions the 5%-noise reaction-diffusion results as supplementary rather than primary evidence.","major_comments":[{"comment":"§3.1 and Tables 3, 5: The headline claim that TGSR-PINN improves parameter recovery over baselines rests on mean±std comparisons without pairwise statistical tests. In Table 3 (n=7), TGSR-PINN's average parameter error of 4.426±3.019% vs. Lightweight FT's 4.825±2.384% is a 0.4 percentage-point difference well within one standard deviation. In Table 5 (n=11), the ν error difference between TGSR-PINN (0.408±0.260%) and Full FT (0.568±0.399%) also has overlapping standard deviations. The paper states it uses a paired comparison protocol (§3.1), so paired data likely exists. The counterfactual ablations (Table 8) do report Wilcoxon tests, but these compare TGSR-PINN against degraded versions of itself, not against the actual baselines. Without pairwise tests against baselines (especially Lightweight FT in the high-Péclet task and Full FT in the cross-PDE task), the improvement-over-baselines","section":null},{"comment":"Table 4 and §3.2: The prominently featured best-α error of 0.38% for TGSR-PINN is selected from 7 repetitions, while the mean α error is approximately 13.25% (per §3.5.3). The paper does note that 'core conclusions still rely on aggregated statistics,' but Table 4 is presented as a standalone comparison table and the 0.38% figure appears in the abstract-level discussion. Given the large gap between best (0.38%) and mean (~13%) α error, the best-repetition result should be more explicitly framed as a ceiling indicator rather than a representative outcome. The risk is that readers interpret 0.38% as typical performance. This is a presentation issue that affects how the central claim is perceived, but it does not invalidate the aggregated evidence.","section":null},{"comment":"§2.2, Eqs. (11)–(21): The method has a substantial number of free hyperparameters: α_s, Δα, β_h, γ_m, γ_min, K, E_ad, ξ, ρ_r, δ_g, and the ΔBIC threshold. The paper provides sensitivity analyses for α_s (Table 12), E_ad (Table 11), and β_h (Table 14), which is commendable. However, Table 11 uses only 2 repetitions per setting, providing weak statistical support for the E_ad=30 default. The paper acknowledges this ('finer task-adaptive step selection is left for future work'), but given that E_ad controls the scoring state on which all downstream steps depend, a stronger sensitivity analysis (more repetitions, or at minimum reporting both individual repetition values rather than just two) would strengthen confidence in the default. This is not necessarily blocking since the main experiments use the default consistently across all methods, but it affects reproducibility confidence.","section":null}],"minor_comments":[{"comment":"Table 5: BitFit's field error of 69.010±13.080% and ν error of 4891±13133% are reported, but these extreme values distort any visual comparison in Figure 5 (log scale). The paper explains this as 'large-scale training instability,' but it may be worth noting whether any BitFit repetitions converged normally or whether all 11 failed, to help readers calibrate the comparison.","section":null},{"comment":"§3.5.4, Table 13: The GMM branch is found to be inactive for most layers in the high-Péclet task (ΔBIC condition not met), making rank fallback the primary route. This is honestly reported, but it raises the question of whether the GMM component adds enough value to justify its complexity. A brief note on whether any task in the paper activates the GMM branch would help readers assess the method's complexity.","section":null},{"comment":"Equation numbering: Eq. (19) defines A_ℓ,j and B_ℓ,j as sub-expressions, but the piecewise definition could be clearer about the transition at ep_ℓ,j = 0.5 (both branches give γ_m at that point, which is consistent but not stated).","section":null},{"comment":"§4.3, Table 16: The computational overhead breakdown reports memory for neuron scoring as ~470 MB, which is the same as the total. This appears to be the peak memory during scoring (forward+backward on frozen model), but the table format makes it look like scoring alone requires 470 MB. A brief clarification would help.","section":null},{"comment":"Figure 8: The aggregated scatter plot of field error vs. parameter error is informative, but the error bars for TGSR-PINN and Lightweight FT overlap substantially in both dimensions. A note acknowledging this overlap would make the figure's interpretation more consistent with the text's cautious framing.","section":null},{"comment":"The paper would benefit from a brief comparison to existing neuron-level pruning or importance estimation methods in the PINN context (e.g., Ref. [35] is cited but the comparison is brief). A paragraph clarifying what specifically differs from selective pruning for PINN inverse problems would strengthen the novelty claim.","section":null}],"recommendation":"major_revision","confidential_remarks":"The stress-test concern about missing pairwise statistical tests against baselines is the most substantive issue. The paper has paired data (stated in §3.1) and reports Wilcoxon tests for ablations, so adding pairwise tests for the main comparisons should be straightforward. The effect sizes are small relative to standard deviations, particularly for the high-Péclet task (Table 3), so the tests matter for the central claim. The cross-PDE task (Table 5) has a somewhat larger relative effect (~28% reduction in ν error) but still has overlapping standard deviations. I would not reject on this basis alone since the ablation evidence is reasonably strong and the method is well-motivated, but the main-experiment statistical gap needs to be addressed before acceptance. The large number of hyperparameters is a secondary concern; the sensitivity analyses are partial but the paper is transparent about limitations."},"author_rebuttal":{"model":"glm-5.2","summary":"We thank the referee for a careful and constructive report. The three major comments are well-taken: (1) pairwise statistical tests against baselines are absent in Tables 3 and 5 and should be added; (2) the best-repetition alpha error of 0.38% in Table 4 needs clearer framing relative to the mean of ~13%; and (3) the E_ad sensitivity analysis in Table 11 uses only 2 repetitions, which is weak. We agree with all three points and will revise accordingly. The referee's positive assessment of the counterfactual ablations, layer-protection and decay-mapping experiments, code availability, and honest discussion of applicability boundaries is appreciated.","responses":[{"response":"The referee is correct. We have paired data from the matched-repetition protocol described in §3.1, and we should have reported pairwise statistical tests against the actual baselines in Tables 3 and 5, not only in the counterfactual ablations (Table 8). We will add Wilcoxon signed-rank tests for the key baseline comparisons: TGSR-PINN vs. Lightweight FT in the high-Péclet task (n=7 paired) and TGSR-PINN vs. Full FT in the cross-PDE task (n=11 paired), as well as the other baseline comparisons. We will report p-values and effect sizes alongside the existing mean±std entries. We acknowledge in advance that some comparisons—particularly the 0.4 percentage-point gap between TGSR-PINN and Lightweight FT in the high-Péclet task—may not reach statistical significance at conventional thresholds given n=7 and the large standard deviations. If that is the case, we will state it plainly and qualify the corresponding claim rather than overstate it. The cross-PDE comparison (n=11, 28.2% relative reduction in ν error) is more likely to reach significance, but we will let the test results speak for themselves. We will also add a note clarifying that the counterfactual ablation tests (Table 8) were designed to answer a different question—whether the benefit comes from target-informed neuron selection versus arbitrary perturbation—rather than to substitute for baseline comparisons.","revision_made":"yes","referee_comment":"§3.1 and Tables 3, 5: The headline claim that TGSR-PINN improves parameter recovery over baselines rests on mean±std comparisons without pairwise statistical tests. In Table 3 (n=7), TGSR-PINN's average parameter error of 4.426±3.019% vs. Lightweight FT's 4.825±2.384% is a 0.4 percentage-point difference well within one standard deviation. In Table 5 (n=11), the ν error difference between TGSR-PINN (0.408±0.260%) and Full FT (0.568±0.399%) also has overlapping standard deviations. The paper states it uses a paired comparison protocol (§3.1), so paired data likely exists. The counterfactual ablations (Table 8) do report Wilcoxon tests, but these compare TGSR-PINN against degraded versions of itself, not against the actual baselines. Without pairwise tests against baselines (especially Lightweight FT in the high-Péclet task and Full FT in the cross-PDE task), the improvement-over-baselines"},{"response":"We agree this is a presentation issue that needs correction. The 0.38% best-repetition α error is a ceiling indicator showing what target-side representation correction can achieve under favorable optimization conditions, not a representative outcome. The mean α error of ~13.25% (reported in §3.5.3) is the representative statistic. We will make the following changes: (1) relabel Table 4 to explicitly state 'best-repetition (ceiling indicator)' in the caption; (2) add the mean α error alongside the best α error in Table 4 so readers see both figures; (3) revise the §3.2 discussion to state upfront that the mean α error is approximately 13.25% and that 0.38% represents the best repetition, not typical performance; and (4) ensure that any abstract-level or summary discussion references the mean rather than the best. We appreciate the referee noting that this does not invalidate the aggregated evidence—the core claims in Tables 3 and 5 are based on mean±std across repetitions, and the counterfactual ablations in Table 8 use 10 paired repetitions with Wilcoxon tests.","revision_made":"yes","referee_comment":"Table 4 and §3.2: The prominently featured best-α error of 0.38% for TGSR-PINN is selected from 7 repetitions, while the mean α error is approximately 13.25% (per §3.5.3). The paper does note that 'core conclusions still rely on aggregated statistics,' but Table 4 is presented as a standalone comparison table and the 0.38% figure appears in the abstract-level discussion. Given the large gap between best (0.38%) and mean (~13%) α error, the best-repetition result should be more explicitly framed as a ceiling indicator rather than a representative outcome. The risk is that readers interpret 0.38% as typical performance. This is a presentation issue that affects how the central claim is perceived, but it does not invalidate the aggregated evidence."},{"response":"The referee's point is valid. E_ad controls the post-adaptation state on which all downstream scoring and selective soft decay depend, so Table 11's 2-repetition sensitivity analysis is insufficient. We will expand this to at least 5 repetitions per E_ad setting (E_ad ∈ {10, 20, 30, 60}) and report individual repetition values alongside the mean. We already report both individual values (Rep A, Rep B) in the current table, so the expanded version will follow the same format with more repetitions. We note that the main experiments use E_ad=30 consistently across all methods, so this does not affect the validity of the main comparisons; the issue is specifically about confidence in the default choice. We also agree that the large number of hyperparameters is a legitimate concern. While we provide sensitivity analyses for the most impactful ones (α_s in Table 12 with 5 reps, β_h in Table 14 with 10 reps, decay mapping in Table 15 with 10 reps), we will add a consolidated hyperparameter table in the revised manuscript listing all defaults, their roles, and which (if any) sensitivity analysis covers them, so readers can assess the overall robustness picture at a glance.","revision_made":"yes","referee_comment":"§2.2, Eqs. (11)–(21): The method has a substantial number of free hyperparameters: α_s, Δα, β_h, γ_m, γ_min, K, E_ad, ξ, ρ_r, δ_g, and the ΔBIC threshold. The paper provides sensitivity analyses for α_s (Table 12), E_ad (Table 11), and β_h (Table 14), which is commendable. However, Table 11 uses only 2 repetitions per setting, providing weak statistical support for the E_ad=30 default. The paper acknowledges this ('finer task-adaptive step selection is left for future work'), but given that E_ad controls the scoring state on which all downstream steps depend, a stronger sensitivity analysis (more repetitions, or at minimum reporting both individual repetition values rather than just two) would strengthen confidence in the default. This is not necessarily blocking since the main experiments use the default consistently across all methods, but it affects reproducibility confidence."}],"tokens_in":24760,"tokens_out":1609,"duration_ms":110279,"standing_objections":[]},"desk_editor":{"model":"glm-5.2","letter":"The main thing to know: this paper proposes a neuron-level scoring and selective soft-decay method for PINN inverse transfer learning, and the core idea is sound. The problem is real — field error and parameter error decouple in PINN inverse problems, and coarse-grained transfer can worsen parameter recovery. The counterfactual ablations (Table 8, Wilcoxon p≤0.037) convincingly show the benefit is not from arbitrary perturbation. Layer protection (Table 14, p=0.002) and the piecewise cubic mapping (Table 15) are well-tested with 10 paired repetitions. The code is public. This is a genuine methodological contribution to a niche but legitimate problem. The stress-test concern about missing pairwise statistical tests against baselines is valid and is the paper's most important weakness. In the high-Péclet task (Table 3, n=7), TGSR-PINN's 4.426±3.019% vs. Lightweight FT's 4.825±2.384% is a 0.4 pp difference — well within one standard deviation. The Allen-Cahn→Burgers result (Table 5, n=11) is similar: 0.408±0.260% vs. 0.568±0.399%, overlapping standard deviations. The paper claims a paired comparison protocol but reports no pairwise tests against baselines. The counterfactual ablations test TGSR-PINN against degraded versions of itself, not against the actual baselines, so they support 'the scoring mechanism matters' but not 'TGSR-PINN significantly outperforms the best baseline.' The 0.38% best-α result (Table 4) is cherry-picked from 7 repetitions where the mean α error is ~13.25%. The GMM branch — a headline component — is inactive in most layers of the primary experiment (Table 13, p=0.593), so the method's main active path is rank fallback. The short-adaptation sensitivity analysis (Table 11) uses only 2 repetitions. Several hyperparameters (γ_m, γ_min, ξ, ρ_r) lack independent ablation. These are real issues but not fatal — the method is principled, the ablations that do exist are well-designed, and the problem framing is correct. The paper is for researchers working on PINN transfer learning or parameter recovery in inverse problems. It deserves a serious referee who can require the pairwise baseline tests, point out the GMM inactivity, and ask for more repetitions on the sensitivity analysis. The central argument holds in principle; the evidence just needs tightening.","headline":"Neuron-level representation correction for PINN inverse transfer learning — method is reasonable, evidence is uneven","tokens_in":25900,"tokens_out":626,"would_cite":false,"duration_ms":27020,"reading_group":"maybe","serious_thinker":"yes","would_accept_peer_review":true},"rs_alignment":null,"lean_confirmation":null,"pith_extraction":{"msc":[],"pacs":[],"model":"glm-5.2","headline":"Soft-decay neurons by target evidence, fix PINN transfer parameters","keywords":[],"falsifier":"If the short-adaptation scoring state is already in a parameter-compensation region, all downstream neuron scores, weak-adaptation signals, and selective soft decay factors operate on contaminated evidence, potentially degrading rather than improving parameter recovery.","tokens_in":24897,"feed_emoji":"🔬","tokens_out":1155,"duration_ms":172370,"temperature":0.7,"pith_summary":"When a physics-informed neural network trained on one PDE is reused for a different but related inverse problem, the transferred weights can look successful — low field-prediction error — while quietly pulling the recovered physical parameters away from their true values. The network compensates for wrong parameters by adjusting its field predictions, so the error metrics decouple: the field looks fine, the parameters are wrong. This paper proposes a method called TGSR-PINN that, after transferring only the network weights (not the source task's physical parameters), runs a short adaptation phase on the target task, scores each hidden neuron for how strongly the target evidence supports keeping it, and then gently scales down — rather than pruning or resetting — the input weights and biases of low-scoring neurons. The central mechanism is a chain: neuron target score (from Taylor sensitivity and pre-activation variance) → weak-adaptation signal (via Gaussian mixture model with rank fallback) → selective soft decay (a bounded, continuous scaling that preserves network topology). The paper claims this target-evidence-driven correction improves physical parameter recovery over full fine-tuning and layer-freezing baselines, with the benefit attributable to informed neuron selection rather than generic weight perturbation.","feed_headline":"Soft-decay neurons by target evidence, fix PINN transfer parameters","feed_subtitle":"A neuron scoring and gentle scaling method cuts physical parameter error in transferred physics-informed networks, where low field error can","key_machinery":"Neuron target score: a per-neuron measure combining first-order Taylor sensitivity of the target loss to the neuron's pre-activation with pre-activation variance, fused geometrically and averaged over fixed scoring batches. Weak-adaptation signal: a continuous value derived from the neuron target score distribution within each layer, estimated via a two-component Gaussian mixture model (with Bhattacharyya-based confidence and BIC-based activation) or a rank-based fallback when GMM evidence is insufficient. Selective soft decay: bounded multiplicative scaling (minimum factor 0.4) applied to the input weight row and bias of low-scoring neurons, preserving network topology and trainability. The","core_discovery":"The paper's central claim is that neuron-level, target-evidence-driven selective soft decay of transferred representations can reduce physical parameter recovery error in PINN inverse transfer learning, and that this benefit is not reducible to general weight perturbation. The key evidence: in a high-Péclet 2D advection-diffusion task, average parameter error drops from 6.582% (Full Fine-Tuning) to 4.426%, with best-repetition diffusion-coefficient error of 0.38% versus 4.06% for the best baseline. In Allen-Cahn-to-Burgers cross-PDE-family transfer, viscosity parameter error drops from 0.568% to 0.408%. Counterfactual ablations with 10 paired repetitions show that randomly decaying neurons (","pith_inferences":["The method's reliance on a 30-step adaptation phase producing reliable neuron scores is a fragility point: if the initial physical parameter guess is far from true, the scoring signal could be contaminated, and the paper's own sensitivity analysis (Table 11) shows substantial variability with only 2 repetitions per setting — the method may benefit from an adaptive or iterative scoring approach tha","The rank-fallback path being the primary active route in the high-Péclet experiments (GMM rarely activates) suggests the GMM branch may be solving a problem that doesn't arise at the network widths tested (100 neurons per layer); it could become more relevant for wider networks or more heterogeneous layer distributions.","The piecewise cubic mapping's superiority over linear, sigmoid, and hard-threshold alternatives (Table 15) hints that the specific shape of the decay function matters less than its bounded, continuous, and monotone character — suggesting a design principle rather than a single optimal function."],"forward_implications":["If selective soft decay works as described, PINN transfer learning for inverse problems can be made safer: practitioners could reuse source-task representations without risking silent parameter compensation, expanding the range of tasks where transfer is beneficial.","The decoupling of field error from parameter error suggests that the PINN community should adopt parameter-level metrics as primary evaluation criteria for inverse transfer, not just field reconstruction accuracy.","The target-scoring mechanism could be applied beyond transfer learning — for instance, diagnosing which neurons in a freshly trained PINN are contributing to parameter compensation versus field fitting, potentially as a training-time diagnostic tool.","If the short-adaptation scoring phase generalizes, the approach could extend to multi-source transfer or neural operator fine-tuning, where identifying which transferred features are target-relevant is even more critical."],"fun_headline_variants":["Selective neuron soft decay reduces PINN transfer parameter error","Target-guided neuron decay improves PINN parameter recovery","Soft decay of transferred neurons recovers PINN physical parameters","Target-evidence neuron decay lowers PINN inverse parameter error","Neuron-level soft decay mitigates negative PINN transfer"],"cache_read_input_tokens":0,"weakest_assumption_plain":"The method assumes that a short 30-step target-adaptation phase produces neuron scores that reliably distinguish target-relevant from target-irrelevant neurons. If the initial physical parameters are far from their true values, this short phase may already enter a parameter compensation region, contaminating all downstream scoring, signal estimation, and decay decisions.","fun_headline_variants_meta":{"raw":{"variants":["Selective neuron soft decay reduces PINN transfer parameter error","Target-guided neuron decay improves PINN parameter recovery","Soft decay of transferred neurons recovers PINN physical parameters","Target-evidence neuron decay lowers PINN inverse parameter error","Neuron-level soft decay mitigates negative PINN transfer","Selective soft decay improves PINN inverse transfer accuracy"]},"model":"glm-5.2","effort":"high","cost_usd":0.0,"raw_usage":{"total_tokens":1511,"prompt_tokens":671,"completion_tokens":840,"prompt_tokens_details":null},"tokens_in":671,"tokens_out":840,"duration_ms":38267,"temperature":1.0,"reasoning_tokens":822,"cache_read_input_tokens":0,"cache_creation_input_tokens":0},"cache_creation_input_tokens":0},"created_at":"2026-07-07T20:17:11.558424+00:00","model_set":{"reader":"glm-5.2"},"falsifier":"If the short-adaptation scoring state is already in a parameter-compensation region, all downstream neuron scores, weak-adaptation signals, and selective soft decay factors operate on contaminated evidence, potentially degrading rather than improving parameter recovery.","supporting_citations":[],"review_version":1}