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Withdrawn from ICLR 2027

Beyond Memorization: Auditing and Generating Functional Neural Weights

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Neural weight generation promises to replace per-task optimization with reusable distribution learning over trained checkpoints, yet rigorous evaluation remains underdeveloped. Task accuracy alone cannot distinguish genuine synthesis from memorization and interpolation. Conversely, parameter-space novelty can arise from nonfunctional dispersion. We introduce WeightAUDIT, a five-metric diagnostic framework that jointly assesses parameter dependence, behavioral dependence, affine interpolation, task utility, and predictive diversity against independently trained references. Auditing nine generators reveals three dominant failure signatures, namely parameter memorization, interpolation, and ineffective generation. We also introduce Weight Diffusion with Instantiated Network Supervision (WINS). It instantiates complete networks from predicted clean weights and backpropagates task loss through these networks to train the denoiser. On KMNIST, WINS achieves 76.9% accuracy, exceeding the training mean of 72.8%, while maintaining weight novelty and predictive diversity near the reference level. Across MNIST, EMNIST, SVHN and CIFAR10, WINS retains utility without severe checkpoint contraction, interpolation, or predictive collapse, although performance varies by dataset. Varying the checkpoint pool size reveals an accuracy dip, followed by higher utility and lower training dependence in larger pools.

Primary area:
generative models
Keywords:
neural weight generation, diffusion models, generative model evaluation, memorization, functional supervision

Reviews

Among:
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1234this paper, Bottom 10%
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_pNbXOpenReview ↗
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1
Confidence
3
Informativeness
1
Presentation
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1
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Paper summary

This paper is an experimental analysis paper which compares different weight generation methods.

The paper makes two contributions:

  1. An evaluation framework called WeightAudit to evaluate neural weight generation algorithms. It consists of 5 different metrics to measure novelty, functional competence, and behavioral diversity.
  2. A novel weight generation method called WINS, which trains a diffusion model to model the parameter distribution of high-performing network checkpoints. Training WINS involves a denoising loss which is computed over a set of model checkpoints (3000 in the experiments) and a supervised task loss which is computed over a subset of the training set of a specific task (2000 samples in the experiments).

The paper provides many experiments on small scale datasets, such as MNIST, KMNIST, EMNIST, SVHN and CIFAR10.

Critical strengths

The paper is in general well written, easy to follow and understand. The experimental protocols are documented well, which is especially important for an experimental analysis paper.

Critical weaknesses

There are several weaknesses to this paper:

Motivation of amortized DNN training The paper motivates neural network weight generation with amortized DNN training. More specifically, that the millions of checkpoints available should be used to learn good (conditional priors) rather than running gradient based training from scratch. Indeed, this is an interesting direction to either speed up training or save energy.

However, this motivation is not reflected in the proposed methods and experimental setup. In fact, WINS proposes an unconditional generator which is dataset and architecture dependent. In practice, WINS requires 3000 trained networks for the exact downstream task and target architecture to train the diffusion model that captures the model weight distribution. This diffusion model is then used to sample new model parameters for exactly the same task and same network architecture. The cost to train this population is excluded from the comparisons (See question 1).

To be of practical relevance, weight generation methods must allow either for cross-dataset or cross-architecture transfer.

Proposed metrics The five proposed metrics include a weight space based metric to measure the similarity of DNNs which is based on the Euclidean distance (Weight Dependence Gap). In experiments, this metric is used to measure novelty, i.e. if the generator memorized the training set. However, this is problematic because:

  1. Heterogenous layer scales Classification layers of CNNs are huge in comparison to the convolutional layers and might dominate the metric (See question 2).
  2. Scaling: Although the authors mentioned to use Git Re-Basin to standardize the checkpoints, this only helps against permutation of the network parameters. However, layers might also be subject to scaling, wich does not effect network behaviour if the network contains layer-norm.
  3. There are further problems for some DNN layers that are not discussed. E.g. the attention mechanism QKTQK^T in transformers is invariant to transformations like WQAW_QA and WKA−TW_KA^{-T} for invertible AA.
  4. Parameter space is not isotropic: Behavioral changes of a DNN when changing the model parameters are typically direction dependent. Small changes in some directions can cause severe performance degradation, while large changes in others can be ignored. This fact is for example used by pruning algorithms that set large parts of a DNN weight vector to zero without degrading its performance (See question 3)
  • Fairness of experiments* WINS leverages 2000 supervised samples to improve parameter generation quality. While the authors state that the other algorithms can have access to these samples as well, it is not obvious if they really do use these samples to compute a task-loss (see question 4).

  • Small scale experiments* Experiments are conducted on very simple datasets that seem inappropriate for an experimental analysis paper in 2026. Even limited compute resources should allow for more realistic setups.

Questions for authors
  1. What is the end-to-end cost of WINS? This means constructing the 3000-checkpoint pool (7.64 GPU-hours according to Appendix G.2) plus generator training, compared with directly training the required number of networks (256). Under what scenario does generation pay off, given that the pool already contains 3000 networks of the target kind? Can the authors show any downstream use of the generated population? Can WINS be conditioned so it generates weights for a dataset or architecture it was not trained on? How would Differentiable Behavioral Supervision work in that case, since it requires labeled data from the target task?

  2. Git Re-Basin removes only permutation symmetry. ReLU rescaling yields WDG = 1.15 for functionally identical networks (Table 9). How do the authors make sure WDG > 1 reflects real novelty rather than unremoved symmetry?

  3. Euclidean distance treats all parameter directions equally, but function changes depend strongly on direction. Did the authors consider function-space or curvature-aware distances?

  4. Is it correct, that baselines are trained on weights only, while WINS also uses labeled task data through the CE term. From the experiments it seems that most of the improvements come from task supervision. Can the authors add the same CE term to the strongest baselines (HyperDiffusion, DeepWeightFlow)?

Reviewer_jbJhOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

Paper Summary

Auditing and Generating Functional Neural Weights investigates whether neural-network weight generators produce useful and diverse networks beyond copying or recombining their training checkpoints. The paper introduces WeightAUDIT, an evaluation framework that combines five reference-normalized diagnostics: nearest-training parameter distance (WDG), error-pattern dissimilarity (BDG), departure from the aligned training affine span (IX), accuracy gain relative to behavior-matched Gaussian perturbations (UG), and within-population predictive disagreement (PD). These measurements aim to distinguish parameter novelty, behavioral novelty, functional utility, and diversity—properties that predictive accuracy alone does not capture.

The paper also proposes WINS, a diffusion-based generator that combines checkpoint denoising with task supervision. Training checkpoints are aligned using permutation matching, standardized, and tokenized into complete weight vectors. A Transformer predicts clean weights from diffusion-corrupted inputs, and the predicted weights instantiate a network whose task cross-entropy is differentiated back into the generator. The resulting objective combines denoising mean-squared error with supervised task loss, encouraging generated networks to retain functional performance while preserving variation learned from the checkpoint population. Generated networks are evaluated without subsequent fine-tuning or accuracy-based filtering.

The experimental study audits nine existing generators in their original settings and compares WINS with seven compatible methods trained on a common KMNIST checkpoint pool. Additional experiments cover five image-classification datasets, with larger target-network evaluations on SVHN and CIFAR10. The authors report that existing generators exhibit different combinations of proximity to training checkpoints, affine-span confinement, and limited utility beyond matched noise. In the common KMNIST setting, WINS achieves a reported mean accuracy of 76.9%, compared with 72.8% for the training checkpoints, while maintaining predictive disagreement close to the training population. Ablations show that diffusion-only training yields poor accuracy, whereas task-loss-only training achieves higher accuracy but substantially reduces diversity. The paper’s principal empirical contribution is therefore a joint evaluation framework and a supervised weight-diffusion method that demonstrates a favorable utility–diversity tradeoff in the tested compact-network settings.

Critical strengths
  • The central motivation is compelling: generated networks can achieve high accuracy while remaining close to training checkpoints, and large parameter distances can arise from nonfunctional perturbations. WeightAUDIT separates parameter-space dependence, error-pattern similarity, affine-span departure, functional utility, and predictive diversity. Evaluating these properties jointly provides a more informative account of generator behavior than accuracy or weight distance alone. The sampling experiments illustrate this distinction particularly well: reducing the number of diffusion steps can improve accuracy while substantially reducing predictive diversity.

  • The paper evaluates its metrics on deliberately constructed populations, including exact checkpoint copies, function-preserving ReLU rescalings, affine averages, Gaussian perturbations, and repeated copies of a held-out network. These controls make the intended interpretation of each diagnostic concrete. The rescaling example is especially useful because it demonstrates that substantial parameter-space displacement can coexist with unchanged predictions. The appendix also explicitly distinguishes normalized diagnostic scores from distributional equivalence and statistical significance, improving the framework’s interpretability.

  • WINS connects the generated parameters directly to task performance by differentiating cross-entropy through the instantiated network. The common KMNIST ablations show why both objective components matter: diffusion-only training achieves 16.5% accuracy, while task-loss-only training achieves 81.8% accuracy but reduces normalized predictive disagreement to 0.01. The combined model achieves 76.9% accuracy with predictive disagreement of 0.99. These results support the proposed combination as an effective way to balance functional quality and diversity in the tested setting. The supervision-strength sweep further characterizes this tradeoff.

  • Protocol II trains compatible generators on the same KMNIST checkpoint pool, reducing variation arising from different source checkpoints. The paper distinguishes held-out networks from held-out images, uses five generator-training seeds, and reports confidence intervals for sweep experiments. It also states that generated networks undergo neither accuracy-based filtering nor post-generation fine-tuning. These choices make the reported results more informative about the generator’s direct output distribution and strengthen the interpretation of the controlled comparisons.

  • The paper specifies target architectures, parameter alignment and standardization, tokenization, diffusion schedules, optimization settings, and baseline adaptations. It also separates checkpoint-corpus construction, generator training, and sampling costs, allowing readers to assess the circumstances under which amortized generation is advantageous. Experiments across five image-classification datasets, together with larger target-network studies on SVHN and CIFAR10, extend the evidence beyond a single benchmark. The explicit acknowledgment of compact-network scope and unresolved controls for the pool-size effect further helps readers interpret the results at an appropriate level of generality.

Critical weaknesses

1- WINS directly optimizes task loss through generated networks, but the experimental comparisons omit closely related supervised generators with explicit diversity mechanisms, such as HyperGAN, which the manuscript discusses in its related work. The CE-only ablation is informative, but its lack of diversity regularization makes it an insufficient substitute for this comparison. Although Appendix F.2 provides all methods access to the same images and labels, equal data access does not establish comparable use of functional supervision. Consequently, the results do not isolate how much of the improvement comes from WINS’s particular diffusion formulation rather than from combining task supervision with a constraint that preserves diversity. A supervised stochastic hypernetwork and a compatible existing generator augmented with the same task loss would provide substantially stronger evidence of the method’s incremental contribution.

2- Appendix D.5 specifies sampling 100 distinct noise anchors without replacement from the training pool, while the pool-size experiments report UG for pools containing fewer than 100 checkpoints, including N=16N=16. These instructions cannot be followed literally, and the manuscript does not explain whether those experiments use fewer anchors, sampling with replacement, or access to a larger checkpoint pool. This is a concrete reproducibility problem, rather than evidence that the reported results are false. Separately, behavior matching selects among only eight noise scales, while the generator comparisons omit the selected scales, actual matching residuals, and raw accuracy denominators. Because UG can become sensitive when training and noise-control accuracies are close, its interpretation requires uncertainty estimates and sensitivity to the noise-control construction.

3- IX is a well-defined residual relative to an aligned training affine span, but query-dependent permutation alignment complicates its interpretation as exclusion of affine generation. An exact affine recombination can move outside the original training span when the generated query is subsequently realigned. Moreover, a small orthogonal perturbation near the training mean can produce a large relative residual despite negligible absolute departure from that span. Other metrics have related interpretive limits: matching error sets does not establish identical predictions, and a reference-level mean nearest-training distance does not exclude a mixture containing copied checkpoints. Although Appendix D.8 acknowledges that the metrics are not distributional certificates, the main-text failure labels should consistently retain that qualification. Absolute residuals, distributional diagnostics, and calibration under the exact alignment pipeline would strengthen these claims.

4- Protocol I does not provide the same level of detail as the common KMNIST experiment regarding checkpoint-pool provenance, pool sizes, independent held-out construction, model selection, and task-specific metric adaptations. These details are essential because the audit’s conclusions depend on the reference populations. For example, HyperDiffusion is evaluated on a 3-D occupancy task and receives a PD score, but the occupancy query set, prediction rule, and diversity reference are not clearly specified alongside the image-based evaluation description. This prevents independent reconstruction of the calculation without establishing that it is incorrect. Per-method audit manifests and raw metric components are needed, and conclusions should be restricted to the configurations actually evaluated.

5- The use of five generator seeds and confidence intervals for sweep experiments is valuable, but the main comparative tables report means without uncertainty for the principal differences or threshold-based classifications. Consequently, small accuracy differences and apparent changes between configurations cannot be assessed reliably. The manuscript also reports dataset- and architecture-specific supervision weights without clearly explaining how those operating points were selected. Excluding audit observations from gradient updates does not establish that they were excluded from hyperparameter selection. The paper should provide per-seed table results, uncertainty for important comparisons, and an explicit validation or prespecified selection procedure. If the audit set informed configuration selection, an untouched final evaluation would be needed to substantiate the resulting profiles.

6- The larger-target experiments do not include competing generators, and WINS remains below the training-checkpoint mean by 5.7 percentage points on SVHN and 8.4 points on CIFAR10 at the largest target size. These gaps deserve direct consideration rather than being absorbed into a categorical “healthy” profile. The SVHN architecture comparison also changes augmentation, preventing its accuracy differences from being attributed solely to model size. Separately, the pool-size sweep changes expected training exposure per checkpoint, pool composition, and reference statistics simultaneously, so the observed accuracy dip does not isolate a causal mechanism. The authors appropriately acknowledge compact-network scope and the need for additional pool-size controls, but broader conclusions require matched-preprocessing comparisons, repeated pool draws, and matched-exposure or longer-training experiments.

Questions for authors

1. Comparison with task-supervised generators.
How does WINS compare with a task-supervised stochastic hypernetwork that explicitly regularizes diversity, such as HyperGAN, under comparable data access, tuning opportunities, and compute? Would WINS retain its advantage if a compatible existing diffusion or flow generator received the same instantiated-network cross-entropy loss? These comparisons would help isolate the contribution of the proposed formulation from the benefit of functional supervision.

2. Noise-anchor construction for small checkpoint pools.
Appendix D.5 specifies 100 distinct noise anchors sampled without replacement, whereas Figure 5 includes training pools smaller than 100 checkpoints. What procedure is used in those cases: fewer anchors, sampling with replacement, or a separate anchor pool? Are the noise anchors, standardization statistics, and alignment references restricted to the available NN checkpoints throughout the sweep?

3. Alignment and the interpretation of IX.
Are generated samples independently realigned before projection onto the training affine span? If so, how does the audit handle an exact affine extrapolation of aligned training checkpoints that moves outside that span after query-dependent permutation matching? Could you report both absolute and normalized residuals, clarify the generation-frame versus post-alignment interpretation, and specify the numerical rank tolerance used for projection?

4. Robustness of the behavior-matched noise baseline.
For the principal generator comparisons, what noise scales are selected, how closely do the selected perturbations match the generated population’s behavioral dissimilarity, and what are the raw training, generated, and noise-control accuracies? Do the UG-based conclusions persist with a finer noise grid and independent anchor/noise draws, particularly when the normalization denominator is small or matching selects an endpoint?

5. Reproducibility of the original-setting.
Could you provide a per-method manifest specifying checkpoint-pool origins and sizes, independent held-out construction, model-selection procedures, code revisions, and evaluation observations? For HyperDiffusion specifically, how are the occupancy query set, hard predictions, and reference population defined when computing PD?

6. Hyperparameter selection and uncertainty.
How were the dataset- and architecture-specific supervision weights and other reported operating points chosen? Were the audit images or held-out checkpoint profiles consulted during selection? Could you provide per-seed results and uncertainty for the main table comparisons, and, if audit observations informed selection, confirm the selected configurations on an untouched evaluation set?

7. Explanation of the pool-size accuracy dip.
Does the reported dip persist across independently sampled checkpoint subsets and under matched per-checkpoint exposure or longer optimization? How much do changes in pool composition, standardization, and audit-reference quantities contribute to the pattern? Which existing results distinguish the proposed interpretation from these alternative explanations?

8. Larger-target performance and practical value.
How should the largest-target accuracy deficits—5.7 percentage points on SVHN and 8.4 points on CIFAR10—be weighed against the favorable diagnostic profiles? Do the architecture comparisons retain their conclusions under consistent augmentation, particularly for SVHN? Could comparisons with a suitable generator at these sizes, or downstream ensemble and uncertainty evaluations, establish when the generated population offers a practical advantage over reusing the checkpoint pool?

Reviewer_EtjKOpenReview ↗
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Confidence
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Informativeness
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Paper summary

The paper introduces WeightAUDIT, a framework for evaluating the novelty, utility, and diversity of generated neural network weights. It also proposes WINS, which adds task supervision to weight diffusion. The authors use WeightAUDIT to assess nine existing generators and evaluate WINS on small CNNs for image classification. Experiments on several image classification datasets show that WINS can generate functional CNNs while maintaining reasonable weight novelty and predictive diversity.

Critical strengths
  • Addresses a useful evaluation gap in the field.
  • The paper is well written and easy to follow. The motivation, proposed metrics, and method are clearly explained.
  • The comparison of nine existing generators offers some interesting findings.
Critical weaknesses
  • I am unsure when WINS would be useful in practice. Its default setup already has 3k trained checkpoints for the same task and architecture. What exacty is the downstream advantage over selecting or reusing models from that pool?
  • Concern on the scalability 1 - the largest generated network has about 114K parameters, while its denoiser has about 63.7M parameters and uses a thousand diffusion steps.
  • Concern on the scalability 2 - Accurracy fall below the training pool on the larger CIFAR10 setting (~10% Acc loss)
  • The paper discusses earlier weight generators such as HyperGAN, but does not evaluate them. Since these methods can generate functional networks without requiring a large pool of pretrained checkpoints, it would be useful to clarify what WINS gains from learning the checkpoint distribution and adding task supervision.
Questions for authors
  1. What's the practical benefit of generating new models when thousands of trained checkpoints are already available? Could you compare WINS with simply selecting models from the existing pool?

  2. How well would WINS scale to larger architectures such as ResNet or ViT? The generator already has 63.7M parameters for a CNN with only 114K parameters.

  3. How expensive is WeightAUDIT itself? Could you report the time and memory needed to compute all five metrics?

  4. How does WINS compare with earlier task-supervised weight generators such as HyperGAN? What is gained by learning from pretrained checkpoints?

  5. Have you explored whether WINS-generated models share similar effective sparse subnetworks, as suggested by the Lottery Ticket Hypothesis?

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

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