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Under review as a conference paper at ICLR 2027

Probabilistic Interpretation of Catastrophic Forgetting via Solution Density

Abstract

In continual learning, standard empirical risk minimization (ERM) can severely degrade a neural network's performance on earlier tasks, which is a phenomenon known as catastrophic forgetting. We study a solution-density interpretation of this behavior: what follows when current-task learning no longer favors low-risk solutions for a distal component of prior data beyond a reference density, and how much prior-task mass can be described in this way? Our framework combines a measure-theoretic risk decomposition with a proximal/distal split relative to the current task. We formulate a solution-density selection hypothesis that bounds the ERM learner's probability of selecting low-risk distal solutions by their normalized parameter volume. Under this hypothesis and label-permutation symmetry, we derive a chance-level lower bound on expected distal risk and a corresponding lower bound on final mixture risk. Within this framework, we further derive an inverse-factorial upper bound of on optimal solution density and selection probability, where is the number of classes with positive distal mass. CIFAR-100 proof-of-concept experiments illustrate the framework across class-disjoint, blurry, and generalized class-incremental settings through empirical risk-CDF comparisons and non-vacuous plug-in risk bounds.

Primary area:
learning theory
Keywords:
continual learning, catastrophic forgetting, measure theory, symmetric group

Reviews

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1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_Pm9XOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
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Soundness
2
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Paper summary

The paper develops a conditional interpretation of forgetting using the reference volume of low risk solutions for prior-task data. A selection hypothesis and label permutation symmetry yield a lower bound on distal risk and on final mixture risk. A separate result bounds exact optimum selection under an additional classwise condition. CIFAR-100 experiments across class disjoint and overlapping tasks compare empirical risk CDFs with the reference and report plug-in risk floors.

Critical strengths
  1. The distinction between the existence of a shared solution and whether training selects it is worth studying. Framing forgetting as a selection problem gives the paper a clear conceptual focus and connects its analysis to an important limitation of simple existence arguments.

  2. The conditional arguments are developed carefully, and the paper is explicit about the assumptions needed for its risk bounds. I also appreciate the additional experiment that chooses thresholds independently of the risk outcomes, since it provides a useful check on the main diagnostic procedure.

Critical weaknesses
  1. The paper is clear that the bound is on final risk, but I still want to see how much performance the model actually loses on old tasks. Please report error on the old examples selected in H.1 just before and after the final task, keeping the mixture weights and evaluation label space fixed. A matched model trained only on that task would help show what the earlier training contributes to the result.

  2. The paper already allows different risk thresholds in Definition 1 and the CDF plots, but the factorial bound only covers exact optima. A small model with a known optimum and a clearly defined reference would let us see how the solution volume grows as we allow a little more error. I'm interested in whether models with useful accuracy are still rare in that example.

Questions for authors
  1. Does the relation to the same reference change between the pre-final and final checkpoints on H.1's fixed final subset, and how does the endpoint compare with a matched current-task-only baseline?

  2. How quickly does reference volume grow as the allowed error increases above the optimum in a small explicit model, and which tolerances still represent useful absolute accuracy?

5 comments

Thank you for your thoughtful and detailed review, especially the concrete suggestions on measuring performance loss and examining near-optimal solution volume. We appreciate your recognition of our framing of forgetting as a selection problem, distinguishing the existence of shared solutions from the probability that sequential training selects them. We are planning to provide a detailed response within the next 48 hours altogether with the requested experimental results and a toy example illustrating how reference solution volume grows with the allowed error. Thank you for your patience.

Thank you for your patience while we completed the additional analysis and experiments.

W1-Q1: Changes in past risk and the contribution of prior training.

We thank the reviewer for asking us to connect final risk to the performance actually lost during the final task. We compare the pre-final checkpoint θN−1\theta_{N-1}, the sequential endpoint θN\theta_N, and a matched current-task-only baseline θonly N\theta_{\mathrm{only}\,N} over 30 seeds per protocol. The baseline uses the same initialization, final-task training set, and final-task training recipe. Across the three models, we hold the evaluation examples, uniform past-task mixture weights, and final evaluation label space fixed. We retain the distal construction from H.1 (I.1 in the revised draft), without reselecting the metric or threshold using these results.

Below, R^\widehat{R} denotes empirical 0-1 risk, and P~(1:N−1)⊥Nε\widetilde{P}_{(1:N-1)\perp N}^{\varepsilon} is the normalized distal component of the past mixture relative to the final task. Tables report means over seeds. Risks are percentages and differences are percentage points.

Table 1. Past risk before and after final-task training.

StatisticCILBlurry1Blurry2gCIL-TVgCIL-UgCIL-L
R^(θN−1;P1:N−1)\widehat{R}(\theta_{N-1};P_{1:N-1})62.4761.9060.7180.0080.2177.42
R^(θN;P1:N−1)\widehat{R}(\theta_N;P_{1:N-1})100.0099.1497.8993.4891.0190.06
R^(θN−1;P~(1:N−1)⊥Nε)\widehat{R}(\theta_{N-1};\widetilde{P}_{(1:N-1)\perp N}^{\varepsilon})62.4758.9054.1077.3680.7975.56
R^(θN;P~(1:N−1)⊥Nε)\widehat{R}(\theta_N;\widetilde{P}_{(1:N-1)\perp N}^{\varepsilon})100.0099.8099.5999.7999.9399.61
Δstep\Delta_{\mathrm{step}}+37.53+37.24+37.18+13.48+10.80+12.64
Δstepε\Delta_{\mathrm{step}}^{\varepsilon}+37.53+40.90+45.49+22.43+19.14+24.05

Δstep=R^(θN;P1:N−1)−R^(θN−1;P1:N−1),\Delta_{\mathrm{step}}=\widehat{R}(\theta_N;P_{1:N-1}) -\widehat{R}(\theta_{N-1};P_{1:N-1}),

Δstepε=R^(θN;P~(1:N−1)⊥Nε)−R^(θN−1;P~(1:N−1)⊥Nε)\Delta_ {\mathrm{step}}^ {\varepsilon} = \widehat{R} ( \theta_N; \widetilde{P} _ {(1:N-1) \perp N} ^ {\varepsilon}) - \widehat{R} ( \theta_{N-1}; \widetilde{P}_{(1:N-1) \perp N} ^ {\varepsilon})

Here, Δstep\Delta_{\mathrm{step}} and Δstepε\Delta_{\mathrm{step}}^{\varepsilon} measure the empirical risk increase across the final task transition, from θN−1\theta_{N-1} to θN\theta_N, on the past mixture and its normalized distal component, respectively. Positive values indicate deterioration.

For CIL, the two comparisons coincide because the entire past mixture is distal. In Blurry and gCIL, final risk is higher on the distal component than on the full past mixture and approaches one. The increase during final-task training is also larger (Δstepε>Δstep\Delta_{\mathrm{step}}^{\varepsilon}>\Delta_{\mathrm{step}}). In four of these five protocols, the distal component has lower pre-final risk despite its higher final risk. These comparisons show both greater endpoint error and a larger loss of predictive performance on the fixed distal component.

Table 2. Effect of prior training on final risk.

StatisticCILBlurry1Blurry2gCIL-TVgCIL-UgCIL-L
R^(θN;P1:N−1)\widehat{R}(\theta_N;P_{1:N-1})100.0099.1497.8993.4891.0190.06
R^(θonly N;P1:N−1)\widehat{R}(\theta_{\mathrm{only}\,N};P_{1:N-1})100.0099.2898.3694.0791.9191.48
R^(θN;PN)\widehat{R}(\theta_N;P_N)17.3917.8517.8262.2853.5653.34
R^(θonly N;PN)\widehat{R}(\theta_{\mathrm{only}\,N};P_N)18.8120.2920.8764.7957.3258.40
Δpast\Delta_{\mathrm{past}}0.00−0.14−0.47−0.59−0.90−1.42
Δcurrent\Delta_{\mathrm{current}}−1.43−2.44−3.05−2.51−3.76−5.06

$ \Delta_{\mathrm{past}} =\widehat{R}(\theta_N;P_{1:N-1})-\widehat{R}(\theta_{\mathrm{only},N};P_{1:N-1}), $

$ \Delta_{\mathrm{current}} =\widehat{R}(\theta_N;P_N)-\widehat{R}(\theta_{\mathrm{only},N};P_N). $

Negative differences favor the sequential endpoint. Prior training yields modest improvements in final-task performance across the six settings and a small advantage on the past mixture in Blurry and gCIL. These gains coexist with the substantial distal risk increases in Table 1.

Q1: Change relative to the same volume reference.

The eCDF figure in Appendix I.1, Figure 7 compares all three models against the same volume reference on the fixed distal subset. Before final-task training, the models achieve markedly lower risks than this reference in every protocol. After final-task training, this advantage largely disappears: the endpoint CDF comparisons are consistent with the selection ordering in Hypothesis 2, with no rejection by the one-sided KS diagnostic at the 0.05 level. The sequential endpoint and the current-task-only baseline exhibit similar mean risks and empirical risk distributions on this subset, despite the substantially lower risk of the pre-final checkpoint. Together, these comparisons suggest that prior training may offer a modest benefit on the final task, while much of its earlier predictive advantage is lost on distal data.

W2-Q2: Solution volume beyond exact optimality.

Thank you for this suggestion. The following small model allows us to calculate how reference volume grows with the permitted excess risk and to relate each tolerance to absolute accuracy.

Consider r≥2r\ge2 equally likely classes, each with a single fixed input vector: Q(X=ei,Y=i)=1/rQ(X=e_i,Y=i)=1/r for i=1,…,ri=1,\ldots,r, where eie_i is the ii-th standard basis vector. Use a bias-free linear softmax classifier with prediction fW(x)=arg⁡max⁡c(Wx)cf_W(x)=\arg\max_c(Wx)_c, parameter region Θ=[0,1]r×r\Theta=[0,1]^{r\times r}, and uniform reference ρ\rho, as in our normalized Lebesgue construction. The optimal 0-1 risk is RQ∗=0R_Q^*=0, attained, for example, by W=IrW=I_r.

For input eie_i, the logits are column ii of WW. Under ρ\rho, each column predicts the correct label with probability 1/r1/r, independently across columns. Thus, the number of misclassified inputs satisfies M(W)∼Binomial(r,(r−1)/r)M(W)\sim\mathrm{Binomial}(r,(r-1)/r), and R(W;Q)=M(W)/rR(W;Q)=M(W)/r. The reference volume allowing excess risk η\eta is therefore

VQ(η):=ρ(S(RQ∗+η;Q))=1rr∑i=0⌊rη⌋(ri)(r−1)i,0≤η≤1.V_Q(\eta) := \rho \left(\mathcal S(R_Q^*+\eta;Q)\right) = \frac{1}{r^r} \sum_{i=0}^{\lfloor r\eta\rfloor} \binom{r}{i}(r-1)^i, \qquad 0 \leq \eta \leq1.

In particular, VQ(0)=r−r≤1/r!V_Q(0)=r^{-r}\le1/r!. For r=10r=10, the model has 100 parameters and chance accuracy is 1010%. The exact formula gives:

Excess risk η\etaRequired absolute accuracy (%)Reference volume VQ(η)V_Q(\eta)
00100%100\%1.0000×10−101.0000\times10^{-10}
0.100.10≥90\ge909.1000×10−99.1000\times10^{-9}
0.200.20≥80\ge803.7360×10−73.7360\times10^{-7}
0.300.30≥70\ge709.1216×10−69.1216\times10^{-6}
0.500.50≥50\ge501.6349×10−31.6349\times10^{-3}

Allowing two mistakes increases the reference volume by a factor of 3,736 relative to exact optimality. Nevertheless, parameters achieving at least 8080% accuracy still occupy only 3.736×10−73.736\times10^{-7} of the reference region. This example shows that, although the solution volume grows substantially with the allowed error, rarity under the reference can persist at useful absolute accuracies beyond exact optimality. We have added this example and its analysis to Appendix K.2 of the revised manuscript.


We hope these additions address your concerns and provide a clearer basis for assessing the contribution of the solution-density perspective. Thank you for the constructive suggestions, which helped us strengthen the empirical evidence and examine solution rarity beyond exact optimality.

Reviewer_tScDOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes a solution-density interpretation of catastrophic forgetting in continual learning. It combines a measure-theoretic decomposition of prior-task risk with a proximal/distal split relative to the current task, and posits a selection hypothesis: on distal prior-task data, sequential ERM assigns no more probability to low-risk solutions than their normalized parameter volume. Under this hypothesis and a label-permutation symmetry, the authors derive a chance-level lower bound on expected distal risk, a corresponding lower bound on final mixture risk, and an inverse-factorial upper bound on the probability of selecting optimal solutions. Proof-of-concept experiments on image-classification benchmarks compare empirical risk distributions of trained models against uniform reference samples, reporting that the resulting risk floors account for a substantial fraction of measured final error.

Critical strengths
  • Framing forgetting as a selection problem — separating the existence of low-risk cross-task solutions from the probability that ERM lands in them — is a conceptually appealing angle that complements loss-landscape and PAC-style upper-bound analyses. The measure-theoretic setup is more careful than typical theory papers in this space.
  • The authors call their experiments "proof-of-concept" and do not oversell; the CDF-based diagnostics and KS tests are a reasonable way to probe the hypothesis qualitatively.
  • The paper is clearly written, with definitions, assumptions, and theorem statements easy to locate, and detailed appendices.
Critical weaknesses
  • Hypothesis 2 (π*_j(S(τ)) ≤ ρ(S(τ)) on distal data) is doing nearly all the work: it is a strong, untestable-in-principle assertion about the measure induced by SGD training versus normalized Lebesgue measure on parameter space. Nothing in the paper derives this ordering from properties of ERM; it is postulated. Theorem 3's "chance-level floor" then follows almost mechanically via stochastic ordering + permutation symmetry. The bound E[R_distal] ≥ 1 − 1/k is exactly the risk of uniform random guessing — a floor one could state for any learner that has "lost its advantage." The theory thus provides a language for forgetting rather than an explanation: whether Hypothesis 2 holds is precisely the scientific question, and the paper offers no mechanism (e.g., drift distance, optimization dynamics, loss-surface geometry) from which the hypothesis would follow.
  • The experiments do not validate Hypothesis 2 as a predictive statement; they select (d, ε) post hoc such that the KS test does not reject, and ε is chosen as "the smallest tested ε with positive mass and non-rejection." Non-rejection by a one-sided KS test with limited samples is weak evidence of stochastic ordering across all τ. Moreover, the "plug-in floor" is computed from the retained distal mass that was itself selected to maximize mass subject to non-rejection — the reported 67.7%–91.1% "error coverage" is therefore not an independently validated bound but a tuned diagnostic. There is no baseline comparison (e.g., does a randomly initialized model, or a model trained with replay, also "pass" the same diagnostic?).
  • Theorem 5 counts equal-volume permutation copies of the optimal set under last-layer symmetry. This is a symmetry counting argument that says little about ERM behavior, since the transfer to the learner's probability relies again on Hypothesis 2 at the optimal-risk threshold — where it is least plausible (hypothesis literally asserts ERM is no better than uniform volume sampling at the optimum). Corollary 6 additionally requires the proximal and distal components to share an optimum, a strong and unverified condition.
  • Single architecture (ResNet-32), single dataset, frozen-feature metric, and no comparison against any continual-learning algorithm (EWC, replay, etc.) — so it is unknown whether the diagnostic discriminates between methods with high vs. low forgetting. Also missing: variance over seeds for Table 1's headline numbers.
Questions for authors
  • Please clarify the difference between a bound on final risk (what you prove) and a bound on forgetting (the increment); the paper's framing occasionally conflates the two.
  • Assumption 3 excludes ties and could fail on degenerate optima; how sensitive is Theorem 5 to near-violations (label mode margin → 0)?
  • For the CIL protocol, the distal mass is 1.000 by construction of the label indicator metric — doesn't this make the CIL row of Table 1 a tautology (final risk ≈ chance level on old classes by definition of class disjointness)?
5 comments

Thank you for the detailed and constructive review. We appreciate your recognition of our framing of forgetting as a selection problem, the careful measure-theoretic formulation, and the clear presentation. We address your concerns below.

W1: A concrete sufficient condition for Hypothesis 2.

Our expected-risk and learner-selection bounds are conditional on Hypothesis 2. We agree that the original presentation needed a concrete setting in which this hypothesis follows from the training objective. To address this, we now provide an explicit sufficient case.

The mechanism is absent-class logit suppression. Earlier training can favor solutions that preserve old-task performance, but current-task optimization can erode this advantage: an old class absent from the current labels still competes in the softmax denominator, so cross-entropy favors lower logits for that class on current-task samples.

Consider end-to-end training with post-ReLU features hψ(x)≥0h_\psi(x)\ge0, logits zc(x)=wc⊤hψ(x)+bcz_c(x)=w_c^\top h_\psi(x)+b_c, and softmax probabilities pc(x)p_c(x) over Yout=C∪O\mathcal Y_{\mathrm{out}}=C\mathbin{\cup}O, where CC and OO are nonempty sets of current and absent output classes. Use one-hot cross-entropy on current-task data as the surrogate loss, with head penalties (λw/2)∑c∥wc∥22+(λb/2)∑cbc2(\lambda_w/2)\sum_c\|w_c\|_2^2+(\lambda_b/2)\sum_c b_c^2, where λw,λb>0\lambda_w,\lambda_b>0 are shared across classes; a backbone-only regularizer is allowed. Writing νj\nu_j for the empirical training distribution, with νj(Y∈C)=1\nu_j(Y\in C)=1, head stationarity at finite parameters gives, for every o∈Oo\in O,

\qquad b_o=-\frac{1}{\lambda_b}\mathbb E_{\nu_j}[p_o(X)]<0.$$ Thus every absent-class logit is negative. Summing the head stationarity equations over all output classes also gives $\sum_{c\in\mathcal Y_{\mathrm{out}}}z_c(x)=0$, so some current-class logit must be positive. The classifier therefore cannot predict an absent old class, yielding $R(\theta;Q)=1$ for any normalized old-task distal component $Q$ supported on $O$. An optimizer law $\pi_j^*$ supported on these head-stationary parameters consequently satisfies $$\pi_j^*(\mathcal S(\tau;Q))=0\le\rho(\mathcal S(\tau;Q)), \qquad 0\le\tau<1,$$ with equality at $\tau=1$. This derives the required ordering from explicit architectural and stationarity conditions. The argument permits end-to-end training and previous-task warm starts. We have added "Example (Absent-class suppression)" after Hypothesis 2 in Section 3.2 and its full derivation in Appendix **H**, and expanded the accompanying "Selection on distal data" remark. **W2-1: Threshold selection independent of risk outcomes.** We agree that selecting thresholds based on the diagnostic can affect the interpretation of its results. Appendix **I.1** provides a complementary experiment in which $\varepsilon$ is selected without using risk CDFs or KS statistics. With the metric fixed, CIFAR-100 test image IDs are split into 20% calibration and 80% evaluation, consistently across task occurrences. For Blurry and gCIL, the threshold is the 95th percentile of distances from final-task calibration samples to the training support; the final past mixture is then evaluated on the separate evaluation subset. Across the five overlapping protocols, this rule retains 58.1%-84.4% of the past mixture, and the resulting plug-in floors account for 53.9%-72.6% of measured final error. These results provide a check on threshold-selection effects; non-rejection alone does not establish the population ordering. We have added a summary of this calibration procedure and its results to the main text. We are also running additional experiments following this approach and will share completed results during the discussion period. **W2-2: Additional experiments with replay.** We plan to extend the proof-of-concept with replay experiments to examine how replay affects the diagnostics and prior-task performance. We will share further analyses during the discussion period as results become available.

W3: Optimal-solution selection and the common-optimum condition.

Theorem 3 and Corollary 4 concern expected risk; Theorem 5 and Corollary 6 additionally quantify the probability of selecting an exact optimum. Theorem 5 separates the geometric and learner-dependent steps:

πj∗(S∗(Q))≤ρ(S∗(Q))≤1r!,\pi_j^* (\mathcal S^* (Q)) \leq \rho (\mathcal S^* (Q)) \leq \frac{1}{r!},

where QQ is a normalized distal distribution covered by Hypothesis 2 and rr counts its classes with positive mass. The first inequality follows from Hypothesis 2, which relates the learner's selection probability to the reference volume. The second is the reference-volume bound obtained from label-permutation symmetry and Assumption 3. The sufficient case in W1 gives a concrete mechanism for the first inequality.

Corollary 6 addresses the compatible case, in which the proximal and distal components admit a common optimum. Writing P1:N=mP~distε+(1−m)P~proxεP_{1:N}=m\widetilde P_{\mathrm{dist}}^\varepsilon+(1-m)\widetilde P_{\mathrm{prox}}^\varepsilon, where m=Pdistε(Z)∈(0,1)m=P_{\mathrm{dist}}^\varepsilon(\mathcal Z)\in(0,1), this condition gives

S∗(P1:N)=S∗(P~distε)∩S∗(P~proxε)⊆S∗(P~distε).\mathcal S^* (P_{1:N}) = \mathcal S^* (\widetilde P_{\mathrm{dist}}^\varepsilon) \cap \mathcal S^* (\widetilde P_{\mathrm{prox}}^\varepsilon) \subseteq \mathcal S^*(\widetilde P_{\mathrm{dist}}^\varepsilon).

Global optimality therefore requires distal optimality under the final learner law πN∗\pi_N^*, so the probability bound transfers. A model that achieves zero risk on the full mixture is one concrete setting satisfying this condition. The implication is that even when a common optimum is representable, the probability that sequential ERM selects a global optimum is at most 1/r!1/r! under the stated assumptions. If the component optima are incompatible, a valid tradeoff optimum may still exist; that case requires a separate analysis.

W4: Broader proof-of-concept and variability across seeds.

To enrich the empirical support for our theoretical analysis, we are running experiments with additional datasets and backbone architectures. We will share completed results during the discussion period and include variability across training seeds for the empirical risk summaries.

Q1: From final-risk floors to forgetting, forgetting measure (FM), and backward transfer (BWT).

We agree that final risk and forgetting are different quantities. Their connection follows by retaining the previously achieved performance as the baseline. Let rj,i=1−aj,ir_{j,i}=1-a_{j,i} denote the risk on task ii after learning task jj, and let NN be the final task index, with Y=Y1:N\mathcal Y=\mathcal Y_{1:N}. Standard forgetting [1] satisfies

=r_{N,i}-\min_{j<N}r_{j,i} \ge r_{N,i}-r_{i,i}.$$ For the choice of $(d,\varepsilon)$ applying to the old-task mixture, the prior-task argument in the proof of Corollary 4 gives $$\frac{1}{N-1}\sum_{i=1}^{N-1}\mathbf E[r_{N,i}] \ge m^\varepsilon_{(1:N-1)\perp N} \left(1-\frac{1}{|\mathcal Y|}\right) =:L_N.$$ Define $\bar r_N=(N-1)^{-1}\sum_{i=1}^{N-1}\mathbf E[r_{i,i}]$, the average expected risk immediately after learning each old task. Consequently, $$\begin{aligned} \mathbf E[\mathrm{FM}_N] \ge L_N-\bar r_N, \ \mathbf E[\mathrm{BWT}_N] \le \bar r_N-L_N. \end{aligned}$$ Thus the distal-mass risk floor translates directly into bounds on forgetting and backward transfer relative to the risk achieved immediately after learning each old task. Expectations are over training randomness. We have added these bounds to Section 3.2, in "Connection to forgetting and backward transfer" immediately after Corollary 4, with the full derivation in Appendix **K.1**. [1] Liyuan Wang, Xingxing Zhang, Hang Su, and Jun Zhu. *A Comprehensive Survey of Continual Learning: Theory, Method and Application*. Section 2.3, Eqs. (3)-(5). **Q2: Sensitivity to small classwise margins.** The bound in Theorem 5 does not deteriorate as the classwise margin approaches zero from above. Its proof uses only strict ordering to establish disjointness of the permuted optimal-solution sets, so the same bound holds for arbitrarily small positive margins under the other stated assumptions. **Q3: Why the CIL diagnostic is not tautological.** In class-disjoint CIL, the label indicator fixes the distal mass at one under our construction, but it does not determine the measured final risk reported in Table 1. Old-class outputs remain among the prediction candidates, so label-disjointness itself does not force old-task errors. The risk CDF ordering in Hypothesis 2 is assessed separately in our experiments and does not follow from the indicator definition. --- Thank you once again for the thoughtful feedback, which has helped us strengthen the paper. We hope the added example and clarifications help address your concerns and convey the contribution of our framework more clearly.

Following our earlier responses to the theoretical concerns, we now provide additional dataset, backbone, and replay experiments addressing the empirical concerns in your review.

Additional backbone: DenseNet-BC-100.

We added CIFAR-100 experiments with DenseNet-BC-100 on CIL, Blurry1, and gCIL-TV (Appendix I.1.1. Diagnostics with DenseNet, Tables 6, 7). We retain the original task splits and distance construction and build a new parameter-volume reference from the DenseNet checkpoints.

Under both the KS and 95th percentile constructions, the one-sided KS diagnostic does not reject the selection relation for the final past mixture in all three protocols. The corresponding plug-in floors amount to 75.14%-92.86% of measured final error under the KS construction and 59.79%-92.61% under the 95th percentile construction.

For the 95th percentile construction, we retain the original distal components and recompute both learner and reference risks using DenseNet. Its mean final distal risks are 1.0000, 0.9992, and 0.9975 for CIL, Blurry1, and gCIL-TV, respectively. These results reproduce the main ResNet findings with a different backbone: severe error on distal components and plug-in floors accounting for a substantial fraction of final error persist under this architecture change.

Additional dataset: ImageNet100.

We extended the proof-of-concept to ImageNet100 with ResNet-18 on CIL, Blurry1, and gCIL-TV, matching the three protocols reported in the DenseNet comparisons. (Appendix I.1.2. Diagnostics on ImageNet100, Tables 8, 9) The experiments use 30 training seeds for CIL and 60 for each overlapping protocol, and the tables include variability across seeds.

Under both the KS and 95th percentile constructions, the selection relation is non-rejected for the final past mixture in all three reported protocols. The plug-in floors account for 75.31%-93.39% of measured final risk under KS and 36.83%-93.15% under the 95th percentile rule. The latter selects thresholds without using risk CDFs or KS statistics and evaluates risks on separate held-out examples.

Table 9 provides the individual-task and past-mixture KS diagnostics, corresponding to the original Table 2. These results extend the empirical scope beyond CIFAR-100, including components with non-negligible mass selected without risk-CDF feedback.

Replay comparisons.

Thank you for suggesting a comparison with replay methods. We added ER and DER++ comparisons on gCIL-TV using 60 matched seeds and buffers of 500 examples, retaining the original KS and 95th percentile constructions. (Appendix I.1.3.)

Risk reduction on the distal component used for ERM. Across both constructions, ER and DER++ reduce distal risk by 13.59-13.68 and 20.79-20.99 percentage points, respectively (Table 11). The one-sided KS diagnostic does not reject Hypothesis 2's selection relation for ERM, but rejects it for both replay learners (Table 10). Replay can therefore overcome the empirical selection disadvantage observed for current-task ERM on the same distal data.

Distal mass reduction with replay support. Separately, at the same metric and threshold, adding the examples actually replayed during the final task shrinks the distal set. Mean distal mass falls from 0.8522 to 0.3167 for both methods under KS, and from 0.8442 to 0.1869 (ER) / 0.1868 (DER++) under the 95th percentile construction (Table 12). Replay thus reduces the portion of the past distribution that remains geometrically separated from the data used for training.

These comparisons show how replayed past-task supervision changes both performance on a fixed distal component and separation from the expanded training support.


The revisions provide a concrete sufficient case for Hypothesis 2, clarify the scope of the theoretical bounds, and establish their connection to standard forgetting metrics. The dataset, backbone, and replay experiments broaden the empirical assessment, alongside threshold calibration without risk-CDF feedback and variability reported across seeds.

We believe these revisions address your main theoretical and empirical concerns, and would appreciate your feedback on any unresolved points before the discussion period ends.

Reviewer_qxgEOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
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2
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Paper summary

This paper studies a solution-density interpretation of catastrophic forgetting: what follows when current-task learning no longer favors low-risk solutions for a distal component of prior data beyond a reference density, and how much prior-task mass can be described in this way. This paper proposes a framework which combines a measure-theoretic risk decomposition with a proximal/distal split relative to the current task. The main contributions can be summarized as:

  1. Formulate a solution-density framework for sequential learning.

  2. Derive a lower bound on expected final risk that scales with distal mass, together with an inverse-factorial upper bound on optimal solution density and selection probability.

  3. Provide a CIFAR-100 proof-of-concept across class-disjoint and overlapping task sequences.

Critical strengths

1.This paper is well written and easy to follow.

2.Interesting ideas. This paperprovides an interesting probabilistic perspective on catastrophic forgetting by connecting the density of low-risk solutions in parameter space with their selection probabilities under sequential ERM.

  1. The theoretical analysis is well structured. Under this hypothesis and label-permutation symmetry, this paper derives a chance-level lower bound on expected distal risk and a corresponding lower bound on final mixture risk, and further derives an inverse-factorial upper bound of 1/r! on optimal solution density and selection probability.
Critical weaknesses

1.Although the paper contains detailed theoretical analysis, the main theoretical results of this article are highly dependent on Hypothesis 2. The author needs to provide a more comprehensive explanation of when and why this hypothesis can hold true in practice.

2.The experimental verification in this paper is limited to the CIFAR-100 and the ResNet-32. I suggest conducting experiments on more datasets and models to further verify whether the relevant conclusions can be applied to more learning scenarios.

3.In the remark on page 7, this paper acknowledges that the proposed bound concerns the final risk, whereas measuring catastrophic forgetting requires comparing the risk before and after learning a new task. However, the final risk lower bound is not equal to the catastrophic forgetting lower bound. More explanations and analyses are needed to prove the correlation between them.

Questions for authors

Please address the concerns in Critical Weaknesses.

2 comments

Thank you for your constructive feedback. We highly appreciate your recognition of our clear presentation, the probabilistic connection between low-risk solution density and selection under sequential ERM, and the structured derivation of the risk and inverse-factorial bounds. We address your concerns below.

W1: When and why Hypothesis 2 can hold.

Previous training can give the learner an advantage on old tasks. For a distal component with little useful supervision or shared structure in the current data, however, current-task learning may fail to preserve this advantage and can even work against it. A concrete mechanism is absent-class logit suppression: old classes absent from the current labels still compete in the softmax denominator, so cross-entropy favors lower logits for these classes on current-task samples. Hypothesis 2 formalizes a regime in which the learner places no more probability on low-risk distal solutions than their reference volume.

This mechanism yields an explicit sufficient condition using the architecture and objective of our experiments. Consider end-to-end training with post-ReLU penultimate features hψ(x)≥0h_\psi(x)\ge0, a softmax head with logits zc(x)=wc⊤hψ(x)+bcz_c(x)=w_c^\top h_\psi(x)+b_c over Yout=C∪O\mathcal Y_{\mathrm{out}}=C\mathbin{\cup}O, where CC and OO are nonempty sets of current and absent output classes, and one-hot cross-entropy on current-task data only. Both head weights and biases are regularized by positive L2L_2 penalties with coefficients shared across classes. At a finite head-stationary point, the head equations give zo(x)<0z_o(x)<0 for every o∈Oo\in O and ∑c∈Youtzc(x)=0\sum_{c\in\mathcal Y_{\mathrm{out}}}z_c(x)=0. Some current-class logit must therefore be positive, so the classifier cannot predict an absent old class. Hence, every such head-stationary parameter has R(θ;Q)=1R(\theta;Q)=1 for any normalized old-task distal component QQ supported on OO. An optimizer law πj∗\pi_j^* supported on these head-stationary parameters therefore satisfies

\qquad 0\le\tau<1.$$ At $\tau=1$, both sides equal one. This establishes a concrete sufficient case of Hypothesis 2, including previous-task warm starts. We have expanded the "Selection on distal data" remark and added "Example (Absent-class suppression)" after Hypothesis 2 in Section 3.2, with the full derivation in Appendix **H**. **W2: Broadening the proof-of-concept.** Thank you for this suggestion. To enrich the proof-of-concept supporting our theoretical analysis, we are currently running experiments on additional datasets and backbone architectures. We will share the results as they become available during the discussion period. **W3: Connection to forgetting, forgetting measure, and backward transfer.** Our prior-task risk bound directly yields bounds on standard forgetting metrics [1]. Following the notation conventions from [1], let $r_{j,i}=1-a_{j,i}$ denote the risk on task $i$ after learning task $j$, and let $N$ be the final task index, with $\mathcal Y=\mathcal Y_{1:N}$. For $i<N$, forgetting $f_{i,N}$ can be written as: $$f_{i,N} =r_{N,i}-\min_{j<N}r_{j,i} \ge r_{N,i}-r_{i,i}.$$ Under the assumptions of Corollary 4, the prior-task argument in its proof gives $$\frac{1}{N-1}\sum_{i=1}^{N-1}\mathbf E[r_{N,i}] \ge m^\varepsilon_{(1:N-1)\perp N} \left(1-\frac{1}{|\mathcal Y|}\right) := L_N,$$ where $m^\varepsilon_{(1:N-1)\perp N}$ is the distal mass of the old-task mixture for the choice of $(d,\varepsilon)$ applying to that mixture. Define $\bar r_N=(N-1)^{-1}\sum_{i=1}^{N-1}\mathbf E[r_{i,i}]$, the average expected risk immediately after learning each old task. Averaging the first inequality and using the definition of backward transfer therefore yields $$\begin{aligned} \mathbf E[\mathrm{FM}_N] &\ge L_N-\bar r_N,\\ \mathbf E[\mathrm{BWT}_N] &\le \bar r_N-L_N. \end{aligned}$$ The forgetting measure (FM) lower bound is the gap between the distal-mass risk floor $L_N$ and the average expected risk $\bar r_N$ immediately after learning each old task; the backward transfer (BWT) upper bound is the negative of this gap. Whenever this floor exceeds the average previously achieved risk, the bounds imply positive expected FM and negative expected BWT. Expectations are over training randomness. We have added these bounds to Section 3.2, in "Connection to forgetting and backward transfer" immediately after Corollary 4, with the full derivation in Appendix **K.1**. [1] Liyuan Wang, Xingxing Zhang, Hang Su, and Jun Zhu. *A Comprehensive Survey of Continual Learning: Theory, Method and Application*. Section 2.3, Eqs. (3)-(5). --- Thank you again for your constructive feedback. We hope the added sufficient case for Hypothesis 2 and the direct connection to standard forgetting metrics address your main theoretical concerns and clarify the contribution of our framework.

Following our earlier responses to the theoretical concerns, we now provide additional dataset and backbone experiments to address the remaining empirical questions raised in your review.

Additional backbone: DenseNet-BC-100.

We added CIFAR-100 experiments with DenseNet-BC-100 on CIL, Blurry1, and gCIL-TV (Appendix I.1.1. Diagnostics with DenseNet, Tables 6, 7). We retain the original task splits and distance construction and build a new parameter-volume reference from the DenseNet checkpoints.

Under both the KS and 95th percentile constructions, the one-sided KS diagnostic does not reject the selection relation for the final past mixture in all three protocols. The corresponding plug-in floors amount to 75.14%-92.86% of measured final error under the KS construction and 59.79%-92.61% under the 95th percentile construction.

For the 95th percentile construction, we retain the original distal components and recompute both learner and reference risks using DenseNet. Its mean final distal risks are 1.0000, 0.9992, and 0.9975 for CIL, Blurry1, and gCIL-TV, respectively. These results reproduce the main ResNet findings with a different backbone: severe error on distal components and plug-in floors accounting for a substantial fraction of final error persist under this architecture change.

Additional dataset: ImageNet100.

We extended the proof-of-concept to ImageNet100 with ResNet-18 on CIL, Blurry1, and gCIL-TV, matching the three protocols reported in the DenseNet comparisons. (Appendix I.1.2. Diagnostics on ImageNet100, Tables 8, 9) The experiments use 30 training seeds for CIL and 60 for each overlapping protocol, and the tables include variability across seeds.

Under both the KS and 95th percentile constructions, the selection relation is non-rejected for the final past mixture in all three reported protocols. The plug-in floors account for 75.31%-93.39% of measured final risk under KS and 36.83%-93.15% under the 95th percentile rule. The latter selects thresholds without using risk CDFs or KS statistics and evaluates risks on separate held-out examples.

Table 9 provides the individual-task and past-mixture KS diagnostics, corresponding to the original Table 2. These results extend the empirical scope beyond CIFAR-100, including components with non-negligible mass selected without risk-CDF feedback.


The revisions provide a concrete sufficient case for Hypothesis 2, connect the risk floor to standard forgetting metrics, and extend the proof-of-concept to ImageNet100 and DenseNet. We believe these additions address the main theoretical and empirical concerns raised in your review. We would appreciate your assessment of the revised analysis and results before the discussion period ends, and we will remain available to clarify any outstanding points.

Comments on the paper

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Summary of responses to the reviewers' main concerns

We thank the reviewers for the constructive feedback. Below we summarize the additional analyses, clarifications, and experiments addressing the main questions and suggestions.

  • A concrete sufficient case for Hypothesis 2. We derive the selection relation from absent-class suppression under explicit architectural and head-stationarity conditions, providing a mechanism grounded in the training objective (Section 3.2; Appendix H).

  • Connection to forgetting measures. We derive bounds on standard FM/BWT metrics and compare paired checkpoints before and after final-task training, quantifying the increase in past risk on both the full past mixture and its distal component (Appendices K.1 and I.1).

  • Threshold calibration without risk-CDF feedback. The 95th-percentile construction selects thresholds without risk CDFs or KS statistics and evaluates risks on separate held-out examples. (Appendix I.1).

  • Additional backbone and dataset. We extend the experiments to DenseNet-BC-100 on CIFAR-100 and ResNet-18 on ImageNet100, covering CIL, Blurry1, and gCIL-TV, with variability reported across seeds (Appendices I.1.1, I.1.2).

  • Comparison with replay. On gCIL-TV, ER and DER++ reduce risk on the same fixed distal component by approximately 14 and 21 percentage points, respectively. Separately, incorporating replayed examples into the training support reduces distal mass at the same metric and threshold (Appendix I.1.3).

We would appreciate your assessment of these responses and supporting results, and clarification of any remaining concerns before the discussion period closes.

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