- Rating
- 3(+1)
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 3(+1)
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Paper summary
The authors propose a new way, called BPI, to evaluate the representation learned by various forward-forward algorithms/backpropagation. In comparison to linear probing which only provides accuracy, BPI quantifies the geometry of misclassified points for a linear probe. A more negative BPI means that the point is more on the side of misclassified class centroid than the side of true class centroid. The authors primarily analyze the distribution of rescue rate (i.e. the proportion of misclassified points that become properly classified after training) at different BPI. The authors find (1) training mostly rescues misclassified points with less negative BPI; (2) local methods that gain more accuracy compared to the untrained network also rescue more; (3) BP rescues gradually over depth, whereas local methods rescue mostly at early layers.
Critical strengths
The rescue rate distribution at different BPI offers a direct description on how representation changes over training and across layers. Authors make an extensive null hypothesis check to isolate the effect of learning algorithms.
Critical weaknesses
The authors claim that they develop a new method to evaluate representation learning and a rescue rate measure as a target to improve local learning. But the benefit of this method is not clear. Specifically:
- It is unclear when using BPI rescue/break rate would be more beneficial than simply using linear probes. As the author points out (line 261-263), rescue rates are consistent with linear probing performance gain. Also, by linearly probing each layer, we could also observe the same conclusion in 2.5: local learning is known to have better decoding accuracy in early layers but struggle to stack.
- It is unclear how the proposed BPI rescue rate could guide better design for improving local learning methods. In particular, BP also shares the trend of better rescuing less negative BPI inputs. And rescue rate for low BPI is not a differentiable target. For example: Yerxa et al., (NIPS 2023) uses manifold capacity (which quantifies the number of object categories that may be represented in a linearly separable fashion) as an objective function to train a network.
Questions for authors
Questions:
- Hyperplanes defined by the linear probes might be heavily influenced by hyperparameters like weight decay and learning rate. How do they influence the result?
- What is the motivation of evaluating pretrained VGG16? What can we conclude from evaluating this model?
- All experiments are performed on convnets and forward-forward local learning methods. Do the conclusions hold when evaluated on other architectures like simple MLP? And other layer-local learning methods, such as greedy layerwise learning (Belilovsky et al., ICML 2020)? I think it is more meaningful to compare different types of local learning instead of different forward-forward algorithms.
- SCFF is fully self-supervised, whereas methods like ASGE is supervised training. There are also other local self-supervised learning: CLAPP (Illing et al., NIPS 2021), LPL (Havagal and Zenke, Nature. Neuro 2023). Are there differences between supervised and self-supervised learning?
5 comments
Further comments on weakness
I thank the authors for their detailed response and extensive additional simulations. My concerns for the questions are properly addressed. Meanwhile, I still have a few comments regarding weakness and writing of the paper:
Weakness 1: I agree that the per-layer contribution ablation is useful for isolate the contribution of local learning algorithm from architecture. This is meaningful because the analysis could change the benchmark comparisons of different local learning algorithms, especially when they use different archictectures. For BPI, which is claimed as an evaluation method, it offers limited insights on local algorithms. I acknowledge that it provides pointwise information and breaks down net accuracy, but it does not tell me about strengths or limitations of particular local algorithms or local learning in general (at least among the algorithms analyzed in the paper). Specifically, for local learning practitioners, why should they also examine BPI in addition to accuracy? For local learning researchers, can BPI be used to justify one method over the other ones? The impact of BPI would be clearer if the authors could use it to make evaluations on the algorithms studied the papers.
Weakness 2: The authors also agree that the paper does not demonstrate how BPI could be used as a target to improve FF/local algorithms. To me, it is neither clear nor promising that BPI could help to design better algorithms. Rather, I would consider it as a potentially useful evaluation method for analyzing the FF/local algorithms in classification tasks. As a result, it would be misleading to define BPI as a target for improvement in the title or abstract, which could give the readers a wrong expectation before reading in detail.
Appendix Writing: The current appendix is difficult to read. I understand the discussion period is too short. If the paper is accepted, I would kindly ask the authors to clean the appendix by (1) careful proofreading to remove weird phrases like "(November 9, 11:50 UTC)" in line 4292; (2) instead of directly flushing paragraphs of details, first summarizing in a few sentences the primary take-away messages for each table and appendix experiment.
W1 (what BPI says about the algorithms). We agree that the usefulness of the analysis should be demonstrated through concrete evaluations of the studied methods. Our results identify differences that aggregate accuracy does not reveal:
- Different local learners at matched accuracy (App. J, Tables A.13–A.14). On the same architecture and from the same initialization per seed, SCFF and DGL have layer-2 probe accuracies of 76.7% and 76.6%, but rescue 14.7% and 9.1% of the untrained network’s errors with BPI < −0.5. Conversely, DGL breaks fewer initially correct predictions far from the boundary (BPI ≥ 0.5: 1.2% vs. 2.2%). Both differences have the same sign at layers 1–3, with the 90% intervals for deep-rescue differences and the 95% intervals for far-boundary breakage differences excluding zero. As both methods are layer-local, locality alone does not explain these differences. At these matched checkpoints, SCFF corrects more deep errors, while DGL better preserves initially correct predictions far from the boundary; neither dominates on both criteria.
- Correction and preservation differ across methods (Apps. J, M). Matched-accuracy comparisons with BP likewise show greater deep-error rescue and greater breakage far from the boundary for SCFF on CIFAR-10, with a similar pattern for SCFF and our LPL instance on STL-10, although some individual comparisons are inconclusive. These are differences between the tested methods and training recipes; they do not establish a general distinction between supervised and self-supervised learning.
- A small accuracy gain can conceal substantial changes (App. J, Table A.12). At layer 3, our HFF re-implementation rescues 14.9% of the CIFAR-10 test set while breaking 12.5%, yielding only a 2.4-point net gain. Separating rescue and breakage reveals this cancellation; conditioning them on BPI further identifies where corrections and failures occur relative to the initial boundaries.
For practitioners, these analyses are useful when the evaluation goal includes correcting errors far inside the untrained network’s incorrect decision regions or preserving its correct predictions. For researchers, they distinguish methods that achieve similar accuracy through different patterns of correction and breakage. They support comparisons against a stated criterion, rather than an unconditional ranking or a claim that greater deep rescue is always preferable.
We have foregrounded these method-specific findings in Section 2.6 and clarified the distinct roles of the analyses: the layer-wise ablation measures what training each layer contributes, rescue and breakage separate changes that net accuracy combines, and BPI locates those changes relative to the reference probe’s decision boundaries.
W2 (title and abstract). We agree that presenting BPI as a target for improving local learning suggests an algorithm-development contribution that we have not demonstrated. We have revised the title and abstract to present BPI as an evaluation tool. The revised title is “Rescuing Points Trapped Inside Incorrect Decision Regions: Evaluating Forward-Forward Learning Beyond Accuracy.”
Appendix Thank you also for the suggestions on the appendix. We have removed operational timestamps, clarified the prose, and added takeaway summaries before experimental details and in table captions.
We thank Reviewer STgN for the constructive feedback. New experiments and revisions are in blue; details and limitations are in Apps. J–M.
W1. What does the protocol add beyond linear-probe accuracy? The protocol uses linear probes, but adds three things that probe accuracy, at one layer or at every layer, does not give.
(1) A layer's own contribution (Fig. 1). Probing each layer of a trained network credits that layer with everything it inherits from the trained layers before it. Our layer-wise ablation instead trains only the first m layers and keeps the rest at their initialization, isolating what training each layer adds beyond its trained predecessors. To our knowledge, such an ablation has not been used to evaluate layer-wise learning methods.
(2) A pointwise answer. Accuracy says how many errors training fixes, not which ones. Conditioning rescue on each error's initial BPI shows what makes a point hard to fix: how deep it lies inside an incorrect region.
(3) Changes that accuracy nets out. Net rescue is exactly the accuracy change, and we agree that Section 2.5 is therefore an accuracy view; we have revised it accordingly. Separating rescue from breakage shows what the net hides: our HFF re-implementation rescues 14.9% and breaks 12.5% of the CIFAR-10 test set at layer 3, a net gain of only 2.4 points. At matched probe accuracy (App. J), BP and DGL rescue fewer errors with BPI <−0.5 than SCFF and break fewer correct examples with BPI ≥0.5, which accuracy cannot show.
W2. How can it guide method development? Rescue is an evaluation target, not a proposed differentiable training loss. The diagnostic can identify concrete goals and assess whether a design change achieves them. We have not demonstrated a new algorithm derived from this diagnostic. The cited manifold-capacity objective is complementary: our protocol can evaluate the representations it produces. We also agree that preferential rescue near the boundary is generic, occurring with BP and untrained controls; the contribution is to quantify what training adds beyond those controls, not to interpret the shared trend as a local-learning-specific failure.
Q1. Sensitivity to hyperparameters (App. K, Table A.16). On SCFF's untrained networks, we tested nine probe variants spanning weight decay, learning rate, dropout, and training duration. The qualitative BPI–rescue relationship persists under every tested variant: near-boundary errors are rescued more often than deeply misclassified errors, although band membership and rescue rates change. App. K gives the details and coverage limits.
Q2. Motivation for pretrained VGG16. It provides a reference trained by end-to-end BP on a large dataset and anchors the ImageNet-1K comparison. It tests whether patterns in BP trained on smaller datasets extend to pretraining and supports the null controls (Section 2.4). On CIFAR-10, its deep rescue does not differ significantly from VGG16 trained from scratch (Table A.10).
Q3. (Apps. L and J). We added a three-hidden-layer ReLU MLP on CIFAR-10, trained from the same initialization per seed with BP, DGL (Belilovsky et al., 2019; 2020), and supervised FF over three seeds, under a protocol committed before the runs. For BP and DGL, near-boundary errors are rescued more often than those with BPI <−0.5 at every layer, as under a second untrained initialization, and both rescue more than that null in every band and layer. At matched accuracy, BP vs. DGL on deep errors (BPI <−0.5) is inconclusive with three seeds, with estimates favoring DGL; FF failed the protocol's minimum-gain criterion and is not analyzed (App. L). On SCFF's architecture, DGL rescues fewer deep errors than SCFF at matched accuracy (App. J). We agree that comparing types of local learning is more informative: the study now covers goodness-based FF, layer-wise cross-entropy, greedy auxiliary-classifier training (DGL), and two self-supervised local methods (App. M), without establishing universality.
Q4. (Apps. J and M). We added CLAPP-s and LPL on STL-10, with SCFF as a reference (App. M). In all three, as for BP and DGL (App. L), rescue rises toward the boundary at every layer, as it does under their untrained nulls, so this trend does not separate supervised from self-supervised learning. At matched accuracy the result is as on CIFAR-10 (App. J): BP rescues fewer deep errors (BPI <−0.5) and breaks fewer correct examples far from the boundary than SCFF or our LPL instance (native 58.1–59.5% vs. 63.2% published), though some comparisons are inconclusive; CLAPP-s could not be matched at every seed. DGL, a supervised local learner, also rescues fewer than LPL, and than SCFF on CIFAR-10, so locality alone does not explain this. Objectives, recipes and data budgets also differ, so these comparisons do not isolate supervision; we report method-specific differences, not a general claim about supervised versus self-supervised learning. App. M gives every outcome and deviation.