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Paper summary
The paper addresses the question of when a learned time-varying representation constitutes a valid dynamical state, in the sense that its present value suffices to determine its future evolution. In the exact setting, closure is formalized through semiconjugacy, meaning that any invertible reparameterization preserves closure under the conjugated flow, but preserving a prescribed mechanistic flow requires that the reparameterization commute with it. For the approximate setting, the authors decompose the latent prediction defect into an irreducible term attributable to the representation itself (the conditional variance of the future latent) and a residual transition-model error. From this they derive two finite-horizon guarantees. First, the current reconstruction error upper-bounds the degree of nonclosure, and second, when the representation fails to determine the future state, the future reconstruction error and the nonclosure cannot simultaneously vanish. The theory is validated on a 16-dimensional synthetic coupled system and on cerebral perfusion MRI, where the proposed PI-TR is compared against a PINN, Mech-ID, and an adapted CITRIS applied without interventions.
Critical strengths
- The question the paper poses is well chosen and clearly articulated. Distinguishing between a representation that merely reconstructs its inputs well and one that actually supports closed autonomous evolution addresses a genuine problem in scientific ML and physics-informed latent modeling, where these two properties are often conflated. The authors' decision to ground this distinction formally in semiconjugacy and lumpability theory, rather than relying on heuristic regularizers, is interesting.
- Theorems 2.4 and Remark 2.5 draw a conceptually clean and valuable distinction, i.e. preserving closure is always achievable through conjugation, whereas preserving a specific mechanistic flow additionally requires the reparameterization to commute with it. This separation offers a useful lens for anyone interpreting identified CRL latents as mechanistic states. That said, the underlying mathematics is fairly elementary, so the contribution here is more clarifying than deep.
- The biomedical testbed constitutes a genuine strength of the paper. Testing on 4D perfusion MRI with a physiologically motivated hidden state is a considerably more demanding evaluation than the rendered benchmarks that dominate temporal CRL work. The authors are also forthright about the method's limitations.
Critical weaknesses
- The paper's central diagnostic (Eq. 3.2) and bounds (Thm 3.3) are never actually used in practice. The main claim is that the framework separates representation-induced nonclosure from transition-model error, yet every experiment reports only the fitted , the quantities , , and are never estimated. This has three consequences. First, the trend observed in the synthetic experiments cannot be attributed to nonclosure rather than merely to a transition model that is harder to fit. Second, the explanation offered via Eq. (4.1) is only conditional, so it falls short of a demonstrated mechanism. Third, nothing in the paper establishes whether the derived bounds are tight or vacuous in practice, leaving the empirical relevance of the theory unclear.
- The theory does not match the paper's main real-world system. Def. 2.2 and Def. 3.1 are formulated for an autonomous flow with fixed parameters , whereas the perfusion system departs from this setting. It is driven by an external input (Eq. D.2), varies from patient to patient while a single transition is shared across them and the transition explicitly receives normalized time relative to the observed concentration peak making it non-autonomous. Moreover, the prescribed mechanistic flow acts on the head outputs rather than on itself. So, an invertible does not actually correspond to the PI-TR architecture. As a result, the paper's central theoretical guarantees are not directly applicable to its own flagship experiment.
- The CRL framing promises more than the paper delivers. The abstract and Sec. 1 position the work as connecting temporal CRL with dynamical systems theory, yet this connection is not substantiated in the manuscript. No identifiability result from the CRL literature is used or proved, and the intersection (Remark 2.5) is never characterized for any concrete case, leaving the purported link between the two frameworks purely formal. Moreover, the CITRIS baseline omits intervention labels, intervention-specific latent partitions, and the intervention-target classifier, stripping away precisely the components that define CRL, which makes it essentially a temporal VAE. The framing therefore overstates the contribution relative to what is actually established.
- The perfusion evaluation has no held-out test set, and model selection and reporting are both performed on the same 7 patients. Checkpoint selection, the start-time and horizon choices, and the reported metrics are all derived from the same 7 validation patients. Furthermore, the 20 seeds share the data split and the pretrained initialization , so the values quantify seed variability only and exclude variability across patients. This matters because most of the reported differences are far smaller than one standard deviation: RMSE vs. , reconstruction versus and defects at Peak and Late roughly for both methods. Reading method rankings into differences of this size is not statistically justified.
- The theoretical novelty is limited relative to the classical and RL literature. Prop. 2.3 is acknowledged as classical, Thm 2.4 follows from two lines of algebra applied to conjugacy, and Eq. 3.2 is the standard conditional-mean decomposition, with (3.5) reducing to a triangle inequality. Closely related notions also appear in model-irrelevance abstractions and bisimulation in RL (Li, Walsh & Littman, 2006; Zhang et al., ICLR 2021), self-predictive representations (Schwarzer et al., 2021; Ni et al., ICLR 2024), which study exactly when the next latent is predictable from the current one, and the Mori–Zwanzig formalism, in which unresolved dynamics manifest as memory and noise terms. The paper should position itself explicitly against these lines of work and state precisely what is new which, as far as I can tell, is mainly (3.4) and its use as a selection criterion in physics-informed modeling.
- Table 2 favors PI-TR by construction and the result on the clinically relevant hidden state is set aside. PI-TR is trained with an ODE trajectory-fitting loss built on the same Euler integrator (with clipping) that also defines the evaluation metric whereas PINN is trained only with finite-difference residuals. So, the comparison is not between methods on equal footing. Moreover, PINN actually performs better on , the unobserved quantity of clinical interest, for . PI-TR's aggregate advantage comes almost entirely from , the very component it is directly trained to fit. Remark 4.1 argues this away, but I believe the issue deserves direct discussion rather than a caveat.
Li et al., Towards a Unified Theory of State Abstraction for MDPs; Zhang et al., Learning Invariant Representations for Reinforcement Learning without Reconstruction; Schwarzer et al., Data-Efficient Reinforcement Learning with Self-Predictive Representations; Ni et al., Bridging State and History Representations: Understanding Self-Predictive RL;
Questions for authors
- Can you report an estimate of (for example, a high-capacity regressor fitted after training to predict from with frozen) next to in the synthetic sweeps, including m = 16? Does the -trend persist in , or is it mostly transition error?
- Can you estimate , and on the synthetic system and show both sides of (3.4) and (4.1)?
- What do patient-level cross-validation and a full start-time × horizon sweep show? Do any CITRIS vs PI-TR differences in Table 1 survive a paired test across patients?
- How do you reconcile the autonomous, fixed assumptions of Sec. 2–3 with the forced, patient-specific, time-conditioned perfusion model? Which theorem, if any, applies to Sec. 4.2?
6 comments
W1/Q2. Are the reconstruction bounds non-vacuous?
Yes, both original bounds can be informative simultaneously. Their usefulness differs across learned representations. We tested the upper bound in Eq. (3.4) and the lower bound in Eq. (4.2) (submitted Eq. (4.1)). Using the same conditional pairs, we estimate as half the mean squared distance between paired future observations. We bound and using the frozen weights and known synthetic flow. The lower bound becomes positive precisely when future-state uncertainty exceeds future reconstruction RMSE.
Table II. Estimated latent nonclosure and its lower and upper bounds at for and .
| Fixed | Future recon. RMSE | bound | bound | Lower bound | Scalar upper bound | ||
|---|---|---|---|---|---|---|---|
| 0.099 | 0.129 | 0.955 | 8.21 | 0 | 0.0011 | 0.424 | |
| 0.484 | 0.124 | 0.855 | 39.57 | 0.0224 | 0.0906 | 10.06 |
The last three columns use the same normalized squared-error scale. This directly tests the explanation in Section 4.1: reconstruction stays near 0.13, but uncertainty rises from 0.099 to 0.484. The lower bound therefore goes from zero to about 25% of the measured nonclosure. Its estimated value is positive in 157 of 275 compressed models.
For the upper bound, the benchmark is the error of always predicting the mean future encoding, ignoring the input. The scalar bound falls below that benchmark in only 3 of 330 learned models; accounting for the direction of reconstruction errors raises this to 92 of 330.
There is also a concrete case where both original scalar bounds are non-vacuous: for the controlled representation at , the lower bound, estimated nonclosure, upper bound, and constant-predictor risk are respectively (raw squared units). The lower bound rules out zero nonclosure, and the upper bound improves on ignoring the input. Appendix F.2 and Table 8 give the calculations and distinguish this result from tightness across the learned models.
W4/Q3. What survives patient-level evaluation and the full start-time × horizon sweep?
The tracer RMSE advantage over CITRIS survives both tests. The original seven validation patients were used for checkpoint selection. In revision,
- We evaluated all 20 original checkpoint seeds on 32 separate ISLES 2017 test patients.
- We also retrained both methods in five folds on 43 distinct development patients, repeating pretraining within each training split and keeping checkpoint-selection patients separate from evaluation patients.
- The full sweep includes every valid start and horizon: 83,660 patient–start–horizon combinations on the test set and 102,005 in cross-validation. We average within patients so that longer scans do not receive greater weight.
Table III. Patient-averaged tracer RMSE and latent defect for CITRIS and PI-TR in held-out testing and five-fold cross-validation.
| Patient-averaged outcome (lower is better) | Evaluation | CITRIS | PI-TR |
|---|---|---|---|
| Eight-frame tracer RMSE | 32 held-out patients | 0.03401 | 0.02394 |
| Eight-frame tracer RMSE | Five-fold CV | 0.04166 | 0.02898 |
| Full-grid tracer RMSE | 32 held-out patients | 0.05134 | 0.02777 |
| Full-grid tracer RMSE, excluding the six submitted settings | 32 held-out patients | 0.05120 | 0.02771 |
| Full-grid latent defect () | 32 held-out patients | 0.0963 | 0.1460 |
| Full-grid latent defect () | Five-fold CV | 0.1046 | 0.2078 |
For the paired Table 1 comparison, PI-TR has lower eight-frame tracer RMSE in 27 of 32 test patients. PI-TR is also lower in 38 of 43 out-of-fold patients. For latent defect, CITRIS was better at both Early horizons. CITRIS also had lower endpoint reconstruction error at all four Peak/Late settings after adjustment. Therefore, the tracer advantage extends beyond the selected settings, while Table 1 does not establish a general PI-TR advantage in latent defect.
Appendix F.3 separates the submitted settings (Table 9), full sweep (Table 10), and cross-validation (Table 11).
W2/Q4. Which theoretical statement applies to perfusion?
The input curve is not part of our fitting process: For each patient, we calculate the entire input curve from the scan before fitting during preprocessing, and hold the patient parameters fixed during each rollout (Appendix E.2).
The learned predictor uses both the current latent state and time relative to the scan peak, so the error decomposition in Eq. (3.2) applies when we condition on both. Theorem 3.3 is tested on the autonomous synthetic system in Section 4.1. In perfusion (Section 4.2), the ODE governs the physiological outputs, and we evaluate how closely those outputs follow it.
W3. What does Theorem 2.4 add to a concrete CRL identification result?
New Corollary 2.6 in Section 2.2 gives an explicit case. On a fixed closed quotient, under the polynomial observation and autoencoder assumptions of Ahuja et al. (2023), exact reconstruction identifies coordinates up to an invertible affine map .
- Every such preserves closure if the flow is transformed with it.
- But if the mechanistic flow is prescribed in the reported coordinates, the admissible maps are exactly those satisfying for every .
This identifies which part of the affine ambiguity remains after the mechanism is fixed. Appendix C states the inherited assumptions; Appendix D.2 proves the corollary. The perfusion CITRIS adaptation has no intervention labels and serves as a temporal variational baseline, not a test of interventional identification.
W5. What is distinct from state abstraction and self-prediction?
We agree that semiconjugacy and the conditional-mean decomposition are established. State abstraction and self-predictive RL likewise ask what a representation must retain to predict its future. Our finite-horizon question is more specific: for a given encoder and decoder, what does observation reconstruction imply about latent nonclosure?
Theorem 3.3 distinguishes two cases: accurate current reconstruction upper-bounds nonclosure, while accurate future reconstruction can force nonclosure to be positive when states sharing the same encoding have different futures. The Q2 measurements above show when that distinction matters numerically.
W6. Does Table 2 establish better hidden-state estimation?
No. PI-TR is trained against the same clipped Euler rollout used for evaluation, while PINN is trained on finite-difference residuals. We checked whether the observed ordering depended on the selected windows: across all 511 eligible start–horizon cells on the 32 test patients, PI-TR had lower mean joint and observed-state () discrepancies, while PINN had lower mean hidden-state () discrepancy in every cell. The joint advantage therefore persists across windows and is driven by .
Thank you for identifying the ambiguity in the original experiments. We clarify that, a larger fitted defect could mean that the representation loses information, or simply that its transition is harder to fit. We now measure these effects separately in
Section 4.1and evaluate both sides of the reconstruction bounds inAppendix F.2. Please also refer to our Global Response for an overview of the revisions. Below, we address your comments and questions point by point.W1/Q1. Does the coupling trend persist after improving the transition?
Yes under compression. The full-dimensional result is different. For each of the 330 trained models, we froze the encoder P, decoder D, and original transition G. On fixed pairs P(x)→P(xτ+), we trained (i) a residual correction G+Hψ, updating only Hψ, and (ii) an independent MLP from scratch. Validation selected the checkpoint and predictor, with the original G also eligible. We evaluated both predictors on the same held-out pairs.
To see what this comparison isolates, write Tτ(G′)=E∥E[Zτ+∣Z]−G′(Z)∥2 for transition-model error, suppressing the fixed P,μ. By
\mathcal R_\tau(G^{\rm opt})=\mathcal E_\tau+\mathcal T_\tau(G^{\rm opt}).$$ The same $\mathcal E_\tau$ appears in both. Thus $\mathcal R_\tau(G)-\mathcal R_\tau(G^{\rm opt})=\mathcal T_\tau(G)-\mathcal T_\tau(G^{\rm opt})$: the reduction isolates removable transition error. To estimate what remains, we also estimated $\mathcal E_\tau$ independently of either predictor. For $m<16$, we sampled pairs of initial states with the same encoding and evolved both. Half the expected squared distance between their future encodings equals the irreducible nonclosure. Each entry below shows $\kappa=0\to1$ **at fixed $m$** (five-seed means; normalized errors $\times 10^3$). **Table I. Original and refitted defects at $\kappa=0$ and $\kappa=1$ across six latent dimensions.** | $m$ | Original defect | Refitted defect | Direct nonclosure estimate | |---:|---:|---:|---:| | 2 | 3.27 → 95.07 | 2.09 → 94.63 | 2.07 → 95.08 | | 4 | 2.00 → 95.22 | 1.69 → 94.94 | 1.64 → 94.69 | | 6 | 1.68 → 93.05 | 1.47 → 92.63 | 1.42 → 91.78 | | 8 | 1.49 → 94.29 | 1.19 → 93.47 | 1.09 → 90.62 | | 12 | 2.02 → 36.32 | 1.34 → 35.20 | 1.08 → 32.62 | | 16 | 1.29 → 2.17 | 0.42 → 0.63 | Inverse check below | At $m=4$, refitting removes only 0.29% of the original defect at $\kappa=1$, and the independently estimated nonclosure tracks nearly the entire increase. At $m=16$, refitting removes 71% at $\kappa=1$. Here we also tested a predictor that uses only $z$ to recover a candidate initial state, evolve it, and encode its future. Its normalized test risk was below $5.3\times10^{-14}$ for every one of the 55 models. This is an achievable prediction risk, whose population value upper-bounds $\mathcal E_\tau$. Therefore, the evidence points to information loss under compression and transition approximation error at full dimension. `Figure 2` shows all 11 coupling values. `Appendices F.1–F.2` give the refit settings, conditional sampler, and larger-sample checks.Eq. (3.2),