- Rating
- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This work presents Principia KAN (PKAN), a KAN‑based symbolic regression method aimed at exact governing‑equation recovery from noisy data. Current KAN‑style symbolic regression has shared‑amplitude‑driven coupling: a global amplitude forces routing probabilities to simultaneously select basis functions and control coefficient sign and magnitude. This constraint frequently produces incorrect equation structures despite low prediction error. PKAN resolves this by decoupling symbolic routing from coefficient estimation. Each dictionary basis candidate gets an independent routing logit and separate signed coefficient; their product forms the effective term contribution, removing restrictions on sign and magnitude for competing basis functions. It applies correlation‑based initialization, standardized features and two‑stage temperature‑annealed training: high‑temperature exploration using only prediction loss, then low‑temperature crystallization with entropy and sparsity regularizers. Two decoding options are provided: direct readout extracting terms from internal model states, and projection‑and‑refit decoding with constrained combinatorial search plus coefficient refitting. Using the Exact Formula Recovery Rate (EFRR) metric that verifies ground‑truth term sets rather than just prediction accuracy, experiments across 600 noisy test conditions show full PKAN reaches 96.83% EFRR, beating genetic‑programming and RL‑based baselines. Ablations validate decoupling improves internal representations, though downstream decoding can partially fix the original coupling issue. Limitations remain including basis collinearity and incomplete dictionaries, and EFRR does not account for algebraically equivalent expressions. In summary, routing‑coefficient decoupling improves term identifiability and exact equation‑recovery performance under noise. (276 words)
Critical strengths
Strength 1: This paper formally defines and geometrically analyzes shared‑amplitude‑driven coupling failure in differentiable dictionary‑based symbolic regression. Beyond empirical results, it reveals a core structural flaw and offers conceptual novelty: it explains noise‑driven model degradation and guides future architecture design, not just proposing another heuristic model.
Strength 2: Its layered evaluation separates internal representation quality from decoder post‑processing. With targeted ablations and the EFRR metric, it disentangles network effects from decoder gains. This rigorous protocol supplies a reusable benchmark template for symbolic‑regression research.
Critical weaknesses
-
PKAN is only validated for additive unary‑basis dictionaries. It lacks experiments for multiplicative terms, nested functions or out‑of‑dictionary targets. Its reported advantages may not generalize to real‑world scenarios, restricting broader adoption of the core insight.
-
The projection‑and‑refit decoder can fix neural‑stage flaws. Though PKAN has better internal representations, final performance partly depends on this post‑processing step. No hyperparameter sensitivity analysis exists, weakening interpretability guarantees. These are revision‑worthy limitations, not grounds for outright rejection.
Questions for authors
1.All benchmarks use ground‑truth terms inside the predefined dictionary. Please supply quantitative results for cases where true terms are missing from the dictionary. How does PKAN’s decoupled design affect exact‑support recovery and false‑term selection under this mismatch, to test limits of your identifiability claim?
-
Projection‑and‑refit decoding uses manually tuned hyperparameters (pool size, scoring weights, coefficient threshold). How stable are key EFRR results when these settings change? Is PKAN’s overall performance partially from decoder tuning instead of decoupled parameterization?
-
PKAN and its shared‑amplitude baseline have different numbers of trainable parameters. Could the direct‑readout EFRR gap stem from larger model capacity rather than decoupling geometry? Did you run capacity‑matched controls to separate these two factors?
-
Projection‑refit fixes direct‑readout errors. How trustworthy are raw routing probabilities p_{ik} when final decoded equations look good? Can you propose practical diagnostics to detect unreliable routing probabilities for end users?
-
The two parameterizations share the same one‑hot hypothesis class but differ in continuous training space. Are there loss landscapes where shared‑amplitude cannot converge to correct one‑hot solutions while PKAN succeeds? Please provide empirical or illustrative examples to support your theoretical motivation.
We thank the reviewer for the careful summary and for noting that these are revision-worthy limitations, not grounds for outright rejection. We answer your five questions directly and state plainly where we have no new data.
[Q1 - out-of-dictionary targets] We did not run out-of-dictionary experiments and have no numbers to report. The identifiability claim is now conditional in Sec. R and Appendix R.3: it holds only when the dictionary is admissible. EFRR is strict equality with the manifest support inside the fixed dictionary (Sec. 3), so for a genuinely outside-dictionary target it is structurally unattainable by definition; the informative quantity would be which substitute terms are selected, which we have not measured. We do not claim otherwise.
[Q2 - decoder hyperparameter sensitivity] We did not run a sensitivity grid and therefore make no stability claim. What we provide is a consolidated list of every active default: Table R1 (Appendix R.1) lists the optimizer and learning rate, the two-phase epoch and temperature schedules, entropy and l1 coefficients, gradient cap, correlation logit scale, normalization floor, direct thresholds, the three-term cap, eight restarts with fixed seed spacing, the projection pool (learned top-6 union univariate top-6) and the refit ridge. Appendix R.1 also identifies which stored result block each setting applies to. Your question of whether the reported EFRR is partly attributable to decoder tuning remains open; we explicitly withdraw any robustness or tuning-independence claim and note that the decoder-only ablation needed to isolate it was not run.
[Q3 - capacity-matched controls] We did not run capacity-matched controls. Sec. 6.3 already concedes that the 217 vs 112 comparison is "without enforcing equal capacity", and Table R2 (Sec. R) states at implementation level what was held fixed (data, dictionary, training-only normalization, routing initialization, optimizer, two-phase schedule, regularizers, eight restarts, direct threshold, support family) and what was not (coefficient block, parameter counts, independent restart streams). We therefore withdraw the causal reading that the 14.83-point gap stems specifically from decoupling geometry rather than capacity or optimization. The supported statement is the narrower one: these two implemented parameterizations differ in internal support identifiability before postprocessing.
[Q4 - how trustworthy are raw routing probabilities] We agree that p_ik is not a posterior and should not be used as one; Sec. 5.5 already says the recovery trace "does not establish causal truth or posterior confidence in the recovered law". This question can be answered without new experiments; Appendix R.3 consolidates the practical diagnostics (also pointed to from Sec. 5.5): (i) residual correlation with proposed terms, the training-domain correlation matrix, singular values and condition number, and reporting sigma_ik and sigma_y beside gamma_ik to separate route preference from magnitude; (ii) direct supports, route margins and training NMSE across the eight restarts, to test whether the layer repeatedly recognizes the same hypothesis; (iii) agreement between direct and projected supports, separating internal recognition from decoder-supplied support. Appendix R.2 documents the row-level audit: the per-condition direct and decoded tables join row by row on dataset and noise level, and the paired outcome counts are 319 / 125 / 36 / 120. A small margin, high restart disagreement, or direct-vs-projected mismatch flags a case where the decoded equation should not be trusted even when it looks good. We make no claim that these are calibrated probabilities.
[Q5 - loss landscapes where shared amplitude cannot reach the correct one-hot solution] This can be answered analytically, with no new experiment, using Appendix A, Prop. 1. For one variable, c = a*p forces every entry to share the sign of a and constrains sum_k |c_k| = |a|. If the target requires two candidates of the same variable with opposite-signed contributions, no finite logits can represent it: the correct one-hot solution lies outside the parameterization's closure, not merely hard to reach. The converse half of Prop. 1 shows the failure is exactly the sign/mass coupling rather than generic optimization difficulty. Geometrically, the coupled coefficient set is a simplex scaled by one signed scalar; the decoupled set is not. This is a representational separation, not a convergence theorem, and Sec. R states that explicitly.
[W1/W2 - additive-only validation and decoder repair] We accept both. The evaluation covers additive unary dictionaries only; multiplicative terms, nesting and out-of-dictionary targets are outside its scope and were not newly tested. The decoder does repair internal errors, which is why both parameterizations reach 96.83%; the revised Sec. 7 withdraws any end-to-end reading.