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Under review as a conference paper at ICLR 2027

A Better Fit Need Not Be a Better Policy: Retraining in Persistent Graph Environments

Abstract

Graph-based predictions can alter the features and outcomes used for later training. We formulate this interaction as a stateful graph-feedback process and compare repeated refitting with continued deployment of the initial classifier. A common-state comparison isolates the contribution of refitting, while a policy comparison also captures the contribution of the graph states generated by deployment. We instantiate the framework in two settings. (i) For synthetic node classification, we establish well-posedness and existence of an invariant distribution, and derive a finite-horizon condition under which lower loss on common states transfers to lower policy loss. Experiments across independently generated synthetic datasets show that fitting and induced-state contributions can reinforce or offset one another. An end-to-end study further shows that the update policy can reverse the performance ordering of GNN architectures. (ii) In a user–product graph simulation, explanation recourse changes product descriptions while historical rating labels remain fixed. Most implemented description edits continue to place the corresponding products above the eligibility threshold after refitting, while aggregate loss changes remain small. These results show that a better fit on an updated graph state may yield a worse deployment policy.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Performative Prediction, Learning on Graphs

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_nEmgOpenReview ↗
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3(+1)
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Paper summary

This paper studies repeated retraining in a persistent graph environment, where predictions affect subsequent features and, in the synthetic setting, outcomes. It distinguishes evaluation using held out data on a common graph state from evaluation along each deployment policy’s own trajectory.

Three main contributions:

  1. An exact decomposition of policy loss differences into contributions from fitting on a common state and from differences in policy induced states.

  2. Results establishing that exact convex refitting is well defined and admits an invariant distribution, a sufficient condition over a finite horizon for preserving a common state advantage between two refitted representations, and a recourse margin condition at a fixed state.

  3. Synthetic evidence about interactions between representations and update policies, including a reversal in the ranking of GCN and skip GCN, and a product description recourse simulation reporting threshold retention separately from aggregate prediction loss.

The claims are evaluated through proofs, simulations on 20 independently generated graphs, a neural extension trained end to end, and a deterministic application using interactions between Amazon users and products.

Critical strengths

S1. The theoretical results appear sound under their stated assumptions, with invariant distribution existence clearly distinguished from convergence and uniqueness.

S2. The GCN and skip GCN ranking reverses across update policies, with a paired interaction of 0.05817 and a 95% interval of [0.04131, 0.07664]. This supports evaluating architecture and retraining jointly.

S3. The convex study handles dependence by averaging five outcome realizations per graph before bootstrapping 20 graphs. The application reports eligibility retention of approximately 88%, 100%, and 94% for R, G, and C, while clearly distinguishing simulated retention from predictive loss and marketplace benefits.

Critical weaknesses

W1. The paper does not directly demonstrate that better held out performance on a common state leads to worse policy loss. The adverse example in Appendix E.6 supports a training objective interpretation, but its corresponding held out decomposition is missing.

W2. The transfer bound is valid under its assumptions, but its usefulness under nonzero feedback remains un demonstrated. Neither the main bound nor the separate refitting versus fixed classifier bound is evaluated in the reported experiments.

W3. The application reports loss differences around 10⁻⁶ but omits the promised numerical sign checks, complete attributions, and solver accuracy evidence. The reported directions therefore cannot be verified from the paper, although the conclusion that aggregate differences are small remains supported.

Questions for authors

Q1. Does “better fit” mean the regularized training objective or held out loss, and does the +0.060152 example have a negative common state fitting term?

Q2. Is there a nonzero feedback example with C_T < Gamma_T, and what information is needed to evaluate the bound for the relevant policy comparison?

Q3. Can the application’s numerical sign certificates, loss attributions, and solver accuracy checks be provided?

5 comments

Thank you for your comments.

W1, Q1

“Better fit” and held-out loss. "Better fit" refers to lower held-out test loss R(f,s)\mathcal R(f,s) on a common state. And yes, in the +0.060152+0.060152 example, the mean fitting contribution is negative: −0.046152-0.046152.

Held-out decomposition. We define the policy gap averaged over rounds t0+1,…,Ht_0+1,\ldots,H as

\coloneqq J_{t_0,H}(\mathrm{refit})-J_{t_0,H}(\mathrm{fixed}).$$ For this example, $(t_0,H)=(600,1000)$. Using the initial classifier $f_0$ as the reference, the fitting contribution $\mathcal R(f_t^{\mathrm{refit}},s_t^{\mathrm{refit}})-\mathcal R(f_0,s_t^{\mathrm{refit}})$ averages $-0.046152$ and the induced-state contribution $\mathcal R(f_0,s_t^{\mathrm{refit}})-\mathcal R(f_0,s_t^{\mathrm{fixed}})$ averages $+0.106304$. The regularized training objective $\mathcal L$ is $0.127136$ lower for the refitted classifier than for $f_0$, with both evaluated on the same current training data. **Experiments.** This example uses five independent graphs with $n=400$ nodes, three outcome realizations per graph, the unscaled two-hop representation $(K=2)$, ridge penalty $\lambda=0.01$, and initial outcomes $y_{i,0}=g_i$, where $g_i$ is the latent group indicator. We average rounds 601–1000 and group realizations within each graph. The fitting-contribution and policy-gap pointwise 95% graph-bootstrap intervals are $[-0.068982,-0.024325]$ and $[0.039277,0.076693]$, respectively. All five graph averages have negative fitting contributions and positive policy gaps. These remain retrospective exploratory estimates from five graphs. Using the primary Bernoulli initialization in this same comparison favors refitting. Appendix E.6 (Table 5, pp. 27–28) now reports the decomposition, setting, and uncertainty. Appendix E.4 (p. 26) specifies the interval calculation, and Section 4.1 (p. 7) highlights the example. > W2, Q2 **(i) Nonzero-feedback example.** On a complete graph with 4 nodes, we compare raw features (A) with one-hop propagated features (B) and refit both classifiers each round. With $\lambda=1$, $(a,c)=(0.1,1)$, and $\varepsilon=0.1$, the two deployments produce different feature states after one round. The common-state advantage is $\Gamma_1\approx0.240969$ and the trajectory term is $C_1\approx0.226933$. Numerical validation showed that $\Gamma_1-C_1>0.0140$. Theorem 1 therefore guarantees lower expected policy loss for A, $J_1(A)<J_1(B)$. Appendix D.4 (pp. 24–25) provides the complete construction and calculation. **(ii) Information needed to evaluate the bound.** To apply Theorem 1, we compute the common-state advantage $\Gamma_T$ and trajectory term $C_T$, then check whether $\Gamma_T>C_T$. To compute $\Gamma_T$, we refit both classifiers on B's states and evaluate their losses on the same test nodes. We average B's loss minus A's loss over B's state distribution and across rounds. To compute $C_T$, we first calculate the expected logit discrepancies $\nu_t$ between these fitted classifiers. We compute $(\mathbf B,\mathbf g,\mathbf c_*)$ from the response parameters, ridge penalty, training/test sizes, and representation bounds, as specified in Appendix D.2. Substituting these constants and $\nu_t$ into Equation (11) yields $C_T$. For the refitting-versus-fixed comparison, we obtain an upper bound on the policy gap by adding the fitting contribution to a bound on the absolute induced-state contribution. We compute the fitting contribution by comparing the refitted and initial classifiers on the refitting policy's states and averaging their loss difference. To compute the induced-state bound, we calculate their expected per-node logit discrepancies $\mathbb E\boldsymbol\delta_t$ on those same states. We evaluate the bound in Appendix D.3, Equation (37), using these discrepancies, the initial classifier $f_0$, graph operators $\mathbf S^K$ and $\mathbf N$, and response parameters.

W3, Q3

We have verified the signed bounds, loss attributions, and fitting accuracy for all three application models. Appendix G.4 (Tables 14–15, pp. 38–40) now reports the complete results, summarized in Section 4.3 (p. 9).

(i) Numerical sign checks and loss attribution. We report the average policy gap over rounds 1–20, Δ0,20\Delta_{0,20}, and the final-round gap, Δ19,20\Delta_{19,20}. Across all 24 comparisons—three representations, four evaluation sets, and two evaluation windows—we found that each interval lies entirely above or below zero, confirming the sign of the corresponding policy gap. For example, R's full-warm average gap is Δ0,20≈5.203546×10−6\Delta_{0,20}\approx5.203546\times10^{-6}, with bounds [4.920683,5.444702]×10−6[4.920683,5.444702]\times10^{-6}. Using the initial classifier f0f_0 as the reference, the fitting and induced-state contributions are 5.525456×10−65.525456\times10^{-6} and −0.321910×10−6-0.321910\times10^{-6}, respectively.

(ii) Solver accuracy checks. We independently recomputed the gradients for all three initial fits and five subsequent refits. Every original fit satisfies ∥∇L∥∞≤2.50×10−9\|\nabla \mathcal L\|_\infty \leq 2.50 \times 10^{-9}. Tightening both the initial fits and subsequent refits yields ∥∇L∥∞≤1.22×10−15\|\nabla\mathcal L\|_\infty\leq1.22\times10^{-15}. Recomputing both policies with these more accurate fits preserves all implemented description sequences, threshold decisions, and 24 loss-gap directions. The largest change in a final or average gap is 4.87×10−94.87\times10^{-9}.


Please refer to the revised manuscript for detailed experimental results


Thank you for the detailed response.

W1, Q1: The held out decomposition answers my question.

W2, Q2: The four node example shows that the condition can hold under nonzero feedback. It covers one round on a very small graph, so the usefulness of the bound in the reported experiments remains open.

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

This paper studies whether repeatedly updating a graph classifier improves its performance when predictions themselves change the data used in later rounds. It compares refitting with keeping the initial model fixed and separates the effects of parameter updates from changes in the graph state. Theoretical analysis and experiments examine these effects, including a reversal in the relative performance of GCN and Skip-GCN under different update policies.

Critical strengths
  1. The paper studies a relevant problem for deployed graph models, where predictions can influence future data. The observed change in architecture rankings gives a concrete reason to consider how a model will be updated when selecting it.

  2. Evaluating models on the same graph state helps distinguish the benefit of refitting from the consequences of earlier predictions. This makes the policy comparisons easier to interpret.

  3. The synthetic experiments use independently generated graphs, paired runs, and confidence intervals. The comparison without feature feedback also helps isolate the role of prediction-induced data changes.

Critical weaknesses
  1. Theorem 1 gives a sufficient condition for model A to outperform model B, but the paper does not show whether this condition holds in the experiments. A numerical example would help demonstrate how the theorem can be used to compare models.

  2. The performance ordering of GCN and Skip-GCN reverses under refitting, but the main experiments fix the magnitude of prediction-induced feature changes. Please vary this magnitude to check whether the reversal persists or depends on the chosen parameter setting.

  3. The product-description experiment assumes that all recommended edits are adopted. Since these edits also affect predictions elsewhere in the graph, partial adoption may lead to different results. Please evaluate different adoption rates to check whether the reported findings still hold.

Questions for authors

The major concerns are already discussed in the weaknesses above.

4 comments

Thank you for your comments and suggestions.

W1

We added a numerical example in which Theorem 1's sufficient condition ΓT>CT\Gamma_T>C_T holds under nonzero feedback.

Numerical example. We take A as the raw representation and B as the one-hop propagated representation (K=1)(K=1), each refitted at every round. We use a complete graph with n=4n=4 nodes, a fixed initial state s0s_0, ridge penalty λ=1\lambda=1, feature-response parameters (a,c)=(0.1,1)(a,c)=(0.1,1), and outcome-resampling probability ε=0.1\varepsilon=0.1. After one round (T=1)(T=1), the common-state advantage is Γ1≈0.240969\Gamma_1\approx0.240969 and the trajectory term is C1≈0.226933C_1\approx0.226933. Interval arithmetic verifies Γ1−C1>0.0140\Gamma_1-C_1>0.0140, establishing lower expected policy loss for A, J1(A)<J1(B)J_1(A)<J_1(B). The deployments also produce different mutable-feature states, with ∥x1A−x1B∥∞≈0.032517\|\mathbf x_1^A-\mathbf x_1^B\|_\infty\approx0.032517.

Section 3.3 (p. 5) replaces the hypothetical illustration with this verified example. Appendix D.4 (pp. 24–25) provides its full specification and calculation.

W2

Dependence on the parameter setting. Our additional experiments show that whether the GCN/skip-GCN ordering reverses depends on the feature-response magnitude cc. At adjustment rate a=0.1a=0.1, the reversal occurs at c=1c=1. At c=0.25c=0.25 and 0.50.5, skip-GCN has lower loss under both policies, while at c=2c=2, GCN has lower loss under both policies.

We retained the original twenty graphs with n=400n=400 nodes and paired outcome randomness. For each architecture, we compare estimated policy losses J600,1000(π)J_{600,1000}(\pi) under the fixed-classifier policy (π=fixed)(\pi=\mathrm{fixed}) and refitting policy (π=refit)(\pi=\mathrm{refit}). These orderings are supported by approximate 95% simultaneous graph-bootstrap intervals adjusted across the fourteen policy-specific comparisons.

Adjustment rate and refitting updates. At c=1c=1, the reversal also persists for adjustment rates a∈{0.05,0.1,0.2}a\in\{0.05,0.1,0.2\} and, at a=0.1a=0.1, when refitting increases from 12 to 36 updates per round.

Appendix F.3 (Tables 10–12 and Figure 6, pp. 32–35) presents every setting and distinguishes architecture ordering under a given policy from each architecture's refitted-minus-fixed policy gap.

W3

Different adoption rates. We evaluated adoption probabilities padopt∈{0,0.25,0.5,0.75,1}p_{\mathrm{adopt}}\in\{0,0.25,0.5,0.75,1\}, using twenty repetitions at each partial-adoption probability. Each repetition lasts H=20H=20 rounds, with independently generated adoption decisions. At each round, each product independently adopts an available recommendation with probability padoptp_{\mathrm{adopt}}. Products that decline can receive recommendations in later rounds. We implement adopted edits simultaneously and update all affected graph representations. Then we compare the fixed-classifier and refitting policies, keeping historical rating labels fixed.

Post-refit threshold retention. We found that most products that adopt a description edit in the first round retain their eligibility after the classifier is refitted. The observed retention rates are 88.8–90.4% for R, 100% for G, and 95.8–95.9% for C under partial adoption, compared with 88.2%, 100%, and 93.8% under full adoption.

Policy losses under partial adoption. We estimate the policy losses J0,20(π)J_{0,20}(\pi) and the refitted-minus-fixed policy gap Δ0,20=J0,20(refit)−J0,20(fixed).\Delta_{0,20}=J_{0,20}(\mathrm{refit})-J_{0,20}(\mathrm{fixed}).

  • Full evaluation set: 144,991 warm test pairs. We compare the policies' average losses over rounds 1–20. At every tested nonzero adoption probability, R and C have slightly higher loss under refitting (Δ0,20>0\Delta_{0,20}>0), while G has slightly lower loss (Δ0,20<0\Delta_{0,20}<0).

  • Smaller evaluation set: 1,820 warm test pairs involving the 124 source-reviewed products. For R, refitting lowers average loss under full adoption. At padopt=0.25p_{\mathrm{adopt}}=0.25 and 0.50.5, the uncertainty intervals include 0. We therefore cannot confidently conclude that refitting improves or worsens R's loss in those settings.

Appendix G.5 (Tables 16–17, pp. 41–42) now presents adoption counts, post-refit threshold retention, and the policy gap Δ0,20\Delta_{0,20} with its fitting and induced-state contributions. It also shows pointwise confidence intervals describing variation across repeated adoption simulations on the same fixed cohort.


Please refer to the revised manuscript for detailed experimental results


Thank you for your valuable feedback that helped us improve our paper.

With the discussion deadline approaching, we wonder whether we have adequately addressed your concerns. We look forward to your response!

Thanks for the detailed response, which addressed my main concerns. I appreciate these efforts and will raise my score.

Thank you for your time and favourable opinion of our paper.

Reviewer_woQtOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper presents common-state and policy-induced-trajectory comparisons for repeated refitting under graph feedback. Induced-state changes can reinforce or offset a fitting advantage, and the preferred neural architecture changes with the update policy. The experimental evaluation shows the effectiveness of the proposed methods.

Critical strengths

S1. This paper proposes a framework for refitting under graph feedback.

S2. The evidence shows the effectiveness of the proposed framework on two graph-feedback settings.

Critical weaknesses

W1. The end-to-end GNN study only covers limited architectures, e.g., GCN and skip-GCN. It will be better to validating the conclusions on more mainstream GNN variants such as GAT and GraphSAGE.

W2. In the evaluation, 400-node graphs are used. How about the experimental results on graphs with different sizes?

W3. The parameter sensitivity could be improved, e.g., the feature adjustment.

Questions for authors

W1-W3

3 comments

Thank you for your feedback.

W1. We evaluated GAT and GraphSAGE under the fixed-classifier policy (π=fixed)(\pi=\mathrm{fixed}) and refitting policy (π=refit)(\pi=\mathrm{refit}) on the original twenty independent graphs, each with n=400n=400 nodes. Both use two message-passing layers and the original fitting settings. We compared the primary feature-response setting (a=0.1,c=1)(a=0.1,c=1) with the no-feature-response setting (a=0)(a=0), keeping the outcome-resampling probability at ε=0.1\varepsilon=0.1. We also increased refitting from 12 to 36 updates per round at the primary setting.

We compare the policy losses J600,1000(π)J_{600,1000}(\pi), which average expected test loss over rounds 601–1000. With 12 refitting updates per round at the primary setting, the estimated policy gap

=J_{600,1000}(\mathrm{refit})-J_{600,1000}(\mathrm{fixed})$$ is $-0.06513$ for GAT, with pointwise 95% interval $[-0.09134,-0.04308]$, and $-0.02876$ for GraphSAGE, with interval $[-0.03749,-0.02055]$. Both the fitting contribution $\mathcal R(f_t^{\mathrm{refit}},s_t^{\mathrm{refit}})-\mathcal R(f_0,s_t^{\mathrm{refit}})$ and the induced-state contribution $\mathcal R(f_0,s_t^{\mathrm{refit}})-\mathcal R(f_0,s_t^{\mathrm{fixed}})$ have negative averages over this window. Both policy-loss benefits also persist with 36 updates. GAT also reverses its mean ordering relative to skip-GCN: skip-GCN performs better under fixed deployment, whereas GAT performs better under refitting. GraphSAGE has the lowest estimated policy loss $J_{600,1000}(\pi)$ among all four GNN architectures under both policies at the primary setting. Without feature response $(a=0)$, GraphSAGE's estimated policy gap $\Delta_{600,1000}$ is $-0.00554$, entirely from fitting. Section 4.2 (Table 2, pp. 7–8) makes this distinction explicit. Appendix F.4 (Table 13, p. 36) presents architecture definitions, policy losses, uncertainty, and fitting-budget comparisons. ---- **W2.** We evaluated graph sizes $n\in\{200,400,800,1600\}$, using twenty graphs at each size and adjusting connection probabilities to keep expected degree near ten. We retained the primary feature-response setting $(a=0.1,c=1)$, outcome-resampling probability $\varepsilon=0.1$, feature and outcome generation, and 60/20/20 split fractions. R/G/C use five outcome realizations per graph; GCN and skip-GCN use one. The estimated policy gaps $\Delta_{600,1000}$ for R/G/C and GCN are negative at every tested size, with pointwise 95% paired graph-bootstrap intervals below zero. The GCN/skip-GCN ordering reversal extends to $n=800$ and $n=1600$: skip-GCN performs better under fixed deployment, whereas GCN performs better under refitting. At $n=200$, the mean ordering follows the same pattern, but the refitting comparison is inconclusive. In the paper's skip-GCN-minus-GCN convention, its interval is $[-0.00836,0.02541]$. Appendix E.8 (Tables 7–8, pp. 29–30) shows graph statistics, policy losses $J_{600,1000}(\pi)$, the decomposition of the policy gap $\Delta_{600,1000}$, and architecture comparisons. Section 4.2 (p. 8) summarizes the findings. Since the training fraction remains fixed, the number of observed training labels $|L|$ increases with graph size $n$; we interpret the results as sensitivity to this joint change. ----- **W3.** We evaluated feature-response magnitudes $c\in\{0.25,0.5,1,2\}$ at adjustment rate $a=0.1$ and adjustment rates $a\in\{0,0.05,0.1,0.2\}$ at $c=1$, varying one parameter at a time. We retained the original preprocessing and initialization. We evaluate R/G/C and GCN/skip-GCN under both policies. For R/G/C, refitting lowers estimated policy loss $J_{600,1000}(\pi)$ at $c=0.5$ and $1$ with $a=0.1$, and across all tested positive adjustment rates at $c=1$. At $(a,c)=(0.1,2)$, G instead has a mean fitting contribution of $-0.021730$ and an induced-state contribution of $+0.055818$. Thus its estimated policy gap $\Delta_{600,1000}$ is $+0.034088$: improved held-out predictions on the common state $s_t^{\mathrm{refit}}$ accompany worse loss along the refitting policy's trajectory. The approximate 95% policy-gap interval adjusted across the 21 R/G/C comparisons is $[0.006206,0.059429]$. At $c=0.25$, all three adjusted intervals for $\Delta_{600,1000}$ include zero. The neural comparison also depends on response magnitude $c$. Skip-GCN has lower loss under both policies at $c=0.25$ and $0.5$. The ordering reverses at $c=1$, while GCN has lower loss under both policies at $c=2$. Appendix E.7 (Table 6, pp. 28–29) and Appendix F.3 (Tables 10–12 and Figure 6, pp. 32–35) report the full comparisons, their fitting and induced-state decompositions, and uncertainty. --- *Please refer to the revised manuscript for detailed experimental results* ---

Thank the authors for their rebuttal. After reading the rebuttal and the revised paper, I tend to keep my positive scores.

Thank you for your positive support.

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