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Under review as a conference paper at ICLR 2027

Estimation of Long-Term Dose-Response via Longitudinal Surrogacy under Time-Varying Confounders

Abstract

Estimating long-term treatment effects is critical in many domains, yet randomized experiments with long follow-up periods are often costly and ethically challenging. Such studies also typically involve dynamic treatment and evolving disease states, and single-visit observation provides little predictive signal for the chronic outcome, such as 90-day mortality given daily treatment for a chronic disease. Existing methods either average the dose, ignore time-dependent confounders, or rely on stringent assumptions. In this paper, we propose a Window-based Sequential Causal Framework (WSCF) that exploits longitudinal surrogates and the treatment path to identify long-term effects across sequential analysis windows. To address time-dependent confounding bias, we learn representations of the history to balance current treatment assignment, while aligning long-term observational data with auxiliary experimental data via optimal transport weighting to adjust for unmeasured confounding. Theoretically, we derive sequential g-formula for identification under a mean exchangeability assumption weaker than prior work, control the rollout error due to estimated surrogates, and establish a generalization bound on counterfactual prediction error. Experiments on synthetic and semi-synthetic datasets from real-world healthcare and online industrial data demonstrate both the effectiveness and long-depth robustness.

Primary area:
causal reasoning
Keywords:
Long-term treatments, Surrogates, Causal inference, Unmeasured confounding, Time-varying confounding

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_S5YTOpenReview ↗
Rating
2
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1
Informativeness
2
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Paper summary
  • WSCF estimates long-term dose-path responses when a continuous dose, covariates and short-term surrogates all evolve over time, fusing a short randomised study without the long-term outcome with a confounded observational cohort: a windowed sequential g-formula identifies the target (Theorems 1–2), per-window optimal-transport weights estimate the surrogate kernel (Theorem 3), a rollout bound is derived under a hard Jacobian constraint, which training encourages through a penalty (Theorem 5), and a generalisation bound collects them (Theorem 6).

  • Validation is by MISE over three replications on a tumour-growth synthetic cohort at six confounding strengths and two semi-synthetic cohorts (MIMIC-III, an industrial panel).

  • The setting is new, the identification chain is careful enough to check, and the paper corrects a flaw in the alignment theory it inherits.

  • The evidence does not yet carry the claims: the margins come with no paired uncertainty, two tables disagree on the same configuration, and no comparison matches the baselines on surrogate information and its use.

Critical strengths

A real and unexplored problem, with an identification argument that is careful enough to check.

  • The setting is new relative to the compared literature and the identification argument can be followed step by step. Specifically, none of the surveyed methods (LEARN, G-Net, CRN, the surrogate-index line) handles time-varying continuous doses, longitudinal surrogates and time-varying confounding together.

The paper corrects a gap in the theory it builds on and states honestly what its own bounds do and do not cover.

  • The counterexample shows that a joint Wasserstein bound does not control the conditional one, contradicting the inequality stated by Theorem 2 of Yang et al. (2024b), and Theorem 3 supplies the missing regularity. Specifically, a density on [0,1]² whose tilt in the surrogate direction flips sign at frequency n has joint W1 → 0 while the integrated conditional W1 stays at a/(3π).

  • The paper is candid about its own limits. Specifically, it says Lemma 4 is "a necessity argument only", that "the penalty is not the condition", and, before Theorem 6, that the generalisation bound excludes weighting error.

Critical weaknesses

The margins over the strongest baselines come without paired uncertainty, and the paper disagrees with itself about the same configuration.

  • The improvements over the strongest baselines lack paired uncertainty estimates, so their robustness across replications is not established. Specifically, against the strongest non-WSCF baseline in each column of Table 1, WSCF improves MISE by 0.005 (βU = 1.0) to 0.041 (MIMIC-III), with per-method standard deviations from three replications of 0.022–0.052 for WSCF and up to 0.090 for baselines; a single method's SD is not the uncertainty of a paired difference, and no paired interval is given.

  • Two tables give different numbers and a different module ranking for one configuration. Specifically, at βU = 3.5 Table 1 gives WSCF 0.504, noOT 0.617 and noIPM 0.506, whereas Table 3 gives 0.479, 0.548 and 0.598, so which module matters changes between tables.

The comparison is not like-for-like, and the strongest natural baseline is missing.

  • No comparison is matched on surrogate information and its use. Specifically, RMSN, CRN, G-Net and DCRN are run "without surrogate pivot" and land at 3.08–3.18 at βU = 3.5, while the paper's own WSCF-noSurrogate ablation scores 2.965; the closeness suggests that how surrogates are used is a major uncontrolled factor, although the methods also differ in model, training and interface, so the gap cannot be attributed to input alone.

  • The baselines that would isolate the contribution are never run. Specifically, G-Net or CRN given the surrogate history as a time-varying covariate and simulated forward is absent, as is a WSCF variant whose surrogate kernel is fitted on the trial alone (n1 = 1500), which is what the OT reweighting must beat.

Questions for authors

See weaknesses.

1 comment
AuthorsOpenReview ↗

Responses to S5YT

Thank you for your comments and suggestions. Please find below point-by-point responses.

  • W1[Paired uncertainty]: A single SD does not reflect the uncertainty of a paired difference. For each Table 1 column, we report 10-seed paired 95% CIs of MISE(strongest non-WSCF baseline) − MISE(WSCF):
β=1.0 · Longitudinal-Sβ=1.5 · LTEEβ=2.0 · LTEEβ=2.5 · LTEEβ=3.0 · LTEEβ=3.5 · LTEEMIMIC-III · Longitudinal-SIndustrial · DRNet
(-0.031, 0.080)(0.051, 0.142)(0.087, 0.141)(0.046, 0.130)(0.059, 0.126)(0.048, 0.140)(0.002, 0.062)(0.117, 0.132)

Most favor WSCF, except at βU=1\beta_U=1, where Longitudinal-S is not significantly different: it uses longitudinal surrogates and debiases time-varying covariates, but not U. Similarly, paired 95% CIs for MISE(WSCF-noOT)−MISE(WSCF) are (-0.049,0.034) at βU=1\beta_U=1 and (0.032,0.166) at 3.5.

  • W2[Table discrepancies]: We apologize for the unclear details. We reran full, noOT, noIPM, noJSR and None from Table3 on a different set of 6 shared seeds for internally consistent ablation comparisons; the new results differ from Table1.

  • W3[w/ vs w/t S]: We apologize for the unclear interpretation of the surrogate pivot's contribution and for overlooking module differences in the comparisons with temporal models (CRN, G-Net, etc.) in Table1. At βU=3.5\beta_U=3.5, we controlled this factor by rerunning all temporal methods previously evaluated without S, now with (w/ S) and without (w/t S) surrogate history, across 6 seeds. We report mean paired MISE differences (95% CIs), MISE(method)−MISE(WSCF).

Modelw/ Sw/t S
RMSN0.167(0.039, 0.294)0.155(0.037, 0.274)
CRN0.241(0.123, 0.358)0.225(0.092, 0.357)
G-Net0.150(0.017, 0.283)0.149(0.029, 0.268)
DCRN0.161(0.051, 0.272)0.169(0.070, 0.267)
WSCF-0.518(0.198, 0.839)

The gap cannot be attributed to input alone, even when surrogate information is matched. Adding S improves G-Net and WSCF but introduces error propagation, causing CRN and RMSN to suffer from variance explosion, while DCRN's design and our JSR penalty suppress this issue, as illustrated in our Related Work section. WSCF still outperforms the other methods with S, showing that JSR, U debiasing, and the window structure also matter.

  • W4[Missing baselines]: CRN and G-Net were given the estimated surrogate history as a time-varying covariate and simulated forward. (CRN retained its adversarial balancing to address time-varying observed confounding, while G-Net has no such debiasing.) At βU=3.5\beta_U=3.5 over 10 seeds, adding surrogate history changed MISE little within either backbone. WSCF beat both adjusted baselines. Holding WSCF's window structure fixed, the variant without the OT debiasing module for hidden confounding still outperforms CRN/G-Net, which simply incorporate S without addressing U, isolating its contribution beyond access to surrogate history.
ModelPaired MISE diff (95% CI)
CRN0.325(0.186, 0.465)
CRN-S0.338(0.205, 0.471)
G-Net0.234(0.099, 0.370)
G-Net-S0.224(0.111, 0.338)
WSCF-noOT0.023(0.001,0.045)

With the same outcome model and kernel-training budget, WSCF achieved lower MISE than the variant whose surrogate kernel was fitted on the trial data alone. This comparison supports adding density-ratio-weighted observational transitions to the trial data.

Reviewer_EzEkOpenReview ↗
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2
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2
Informativeness
2
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2
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Paper summary

This paper provides a method for estimating long-term dose-response curves when treatment is a continuous dose that changes over time, and the long-term outcome is only observed in confounded observational data. The setting combines two data sources: a large observational dataset that contains the long-term outcome but suffers from hidden confounding, and a smaller randomised trial that observes short-term surrogates but not the long-term outcome. The basic idea is to learn how the surrogates evolve under a given dose path from the trial, learn how the long-term outcome depends on a recent window of surrogates from the observational data, and combine the two appropriately. To do this, the authors re-weight the observational data with optimal transport to match the trial, balance the treatment history to handle observed confounding, and penalise the model’s sensitivity to its own past predictions so that errors are controlled when predicted surrogates are fed back in. The key assumptions are: 1) the relationship between surrogates and the long-term outcome is the same in both data sources, 2) only a finite window of past surrogates matters, and 3) surrogates don’t feed back into future doses or covariates. They provide synthetic and semi-synthetic experiments to test their method.

Critical strengths

The problem is important and the motivating example provides a clear outline of why the work is needed: it shows that how much the dose oscillates, rather than its average level, is what carries signal. I also found the counterexample showing that a bound in prior work (Yang et al., 2024b) does not hold without extra regularity to be a useful contribution.

Critical weaknesses

I’m struggling a little to understand what the optimal transport reweighting adds. The weights are chosen so that the reweighted observational data matches the trial data, including the current surrogate. If so, the surrogate dynamics are really just being learned from the trial. Since the weights are themselves estimated from the trial samples, I don’t see how the reweighted observational data can tell us more about the trial dynamics than the trial data alone. Can you help me understand what this buys over simply fitting the surrogate model on the trial data? I would be interested in seeing that baseline.

My reading is that most of the work is then being done by the assumption that the surrogate-to-outcome relationship is the same in both data sources. This effectively requires the hidden confounder to affect the outcome only through the surrogates. Is this reading correct? In the synthetic data, the outcome doesn’t depend on the hidden confounder directly, so this assumption holds by construction. It would be quite instructive to see how the method performs when a direct effect of the confounder on the outcome is added. Relatedly, in the synthetic data the covariates include lagged surrogates, and the dose depends on the covariates. This seems to violate the assumption that surrogates don’t feed back into future doses or covariates. Am I misreading this?

Finally, the improvements over baselines are small relative to the standard errors (e.g. 0.504 vs 0.528 at \beta_U = 3.5), and at \beta_U = 1.0 the version of the model with all components removed does best. The ablation numbers in Table 3 also don’t match Table 1 for the same setting. Some explanation of these discrepancies, would help.

If these points could be addressed adequately I would raise my score.

Questions for authors

The penalty that keeps the model insensitive to its own past predictions makes sense for controlling error, but it forces the learned dynamics to forget the past quickly. The motivating example, tumour growth, doesn’t obviously behave this way. Can you comment on the trade-off here, and whether the penalty could hurt when the true dynamics have long memory?

I also found the paper quite hard to read in places. The same symbols are reused for different things, and some assumptions are stated differently in the main text and the proofs. One thing that would improve readability would be a short, plain description early on of what each component of the method is for, and which source of bias it addresses.

2 comments
AuthorsOpenReview ↗

Response to EzEk comments of Weakness

Thank you for your comments and suggestions. We apologize for the confusion. Please check point-by-point responses.

  • W1[OT and trial alone]: As in the Preliminary, short-term trials cannot collect long-term Y due to budget/ethical limits (e.g., patients cannot be forced onto a 10-year placebo); OBS data provide Y. Training on trial data alone is unrealistic without observed Y. At βU=3.5, 3-seed MISE is 0.517(0.024) for WSCF-datafusion vs 0.678(0.112) for WSCF-trialalone, worse due to n1≪n0n_1\ll n_0. Both datasets collect S, so unbiased trial surrogate dynamics help debias OBS via OT reweighting, enabling unbiased Y extrapolation D0→D1. If regulations/budgets allowed long-term trial follow-up, D1 alone would suffice without an external long-term D0.
  • W2[U-Y direct effect]: As shown in the Fig.4 causal diagram and A4 mean exchangeability, U affects Y only indirectly via A and S. We add an experiment where U also directly affects Y, Yt=βY0+1δ∑j=0δ(βYL,j⊤Lt−j+βYS,j⊤St−j+βYU,j⊤Ut−j)+εY,t.Y_t=\beta_{Y0}+\frac{1}{\delta}\sum_{j=0}^{\delta} (\beta_{YL,j}^{\top}L_{t-j}+\beta_{YS,j}^{\top}S_{t-j} +\beta_{YU,j}^{\top}U_{t-j})+\varepsilon_{Y,t}. At βU=1,3.5,4, WSCF MISEs are 1.254,1.961,2.006. We report 10-seed mean paired differences (95% CIs), MISE(method)−MISE(WSCF): |Method|βU=1.0|βU=3.5|βU=4.0| |---|---:|---:|---:| |G-Net|0.334(−0.110,0.778)|0.338(0.016,0.660)|0.496(0.214,0.779)| |CRN|0.485(0.033,0.937)|0.472(0.183,0.762)|0.586(0.313,0.859)| |LIRL|−0.118(−0.565,0.328)|−0.142(−0.391,0.108)|0.086(−0.186,0.357)| |LEARN|5.425(3.786,7.065)|3.743(2.880,4.607)|3.132(2.458,3.806)| |Longitudinal-S|0.272(−0.245,0.789)|0.488(0.134,0.841)|0.626(0.246,1.005)| |WSCF-None|0.304(0.021,0.586)|0.623(0.331,0.916)|0.716(0.474,0.958)| |WSCF-noOT|−0.224(−0.624,0.176)|0.488(0.211,0.764)|0.393(0.099,0.686)| |WSCF-noJSR|−0.081(−0.369,0.208)|0.093(−0.200,0.385)|0.222(0.003,0.441)| |WSCF-noIPM|−0.098(−0.469,0.274)|0.408(0.083,0.734)|0.365(0.087,0.644)|

Broader gains under direct U-Y effects may require larger βU than in the indirect setting. Most CIs favor WSCF, with significant gains growing with βU, except LIRL, whose results are nonsignificant. LIRL's hidden-confounding debiasing uses an extra auxiliary variable over WSCF; transferring one LL to the auxiliary variable would roughly downgrade its results to WSCF-noJSR. The choice needs prior domain knowledge, and a wrong choice may violate identification assumptions. Direct U-Y effects may also underlie the outcomes in MIMIC-III and Industrial data.

[lag_S vs assumptions]: We apologize for the imprecise statement of A6. The name "No surrogate feedback" was misleading. Extending Longitudinal-S (Huang et al., 2026) and the proofs of Lemma 1 and Thm1 & 2, we restate A6 as "Conditional Independence from Future" to reflect the temporal ordering and maintain consistency with the other assumptions. St(aˉt)⊥Ht′′∣St′(aˉt′),Hˉt′,G=1,∃ t′<t−δ, ∀ t′′>t.S_t(\bar a_t)\perp H_{t''}\mid S_{t'}(\bar a_{t'}),\bar H_{t'},G=1, \quad \exists\,t'<t-\delta,\ \forall\,t''>t. There always exists a sufficiently early time t′t' such that, conditional on the past surrogate St′S_{t'} and the history up to t′t', the current potential surrogate St(aˉt)S_t(\bar a_t) is independent of future doses A and covariates L. Thus, A6 allows a lagged surrogate to be included as a covariate.

  • W3[Small Improvements]: Per-method SDs are not the uncertainty of a paired difference. For each Table1 column, we report 10-seed paired 95% CIs of MISE(strongest non-WSCF baseline) − MISE(WSCF):
βU=1.0 Longitudinal-SβU=1.5 LTEEβU=2.0 LTEEβU=2.5 LTEEβU=3.0 LTEEβU=3.5 LTEEMIMIC-III Longitudinal-SIndustrial DRNet
(-0.031, 0.080)(0.051, 0.142)(0.087, 0.141)(0.046, 0.130)(0.059, 0.126)(0.048, 0.140)(0.002, 0.062)(0.117, 0.132)

Most favor WSCF, except at βU=1\beta_U=1, where Longitudinal-S is not significantly different: it uses longitudinal surrogates and debiases time-varying covariates, but not U. Similarly, paired 95% CIs for MISE(WSCF-noOT)−MISE(WSCF) are (-0.049,0.034) at βU=1\beta_U=1 and (0.032,0.166) at 3.5. [WSCF-None at βU=1\beta_U=1] Thank you for pointing out WSCF-None's unexpected result at βU=1\beta_U=1. We found a coding error for noIPM/None variants: IPM debiasing was removed only from the outcome model instead of both S&Y models. (All newly added experiments involving None and noIPM variants are corrected.) Corrected 10-seed paired 95% CIs for MISE(ablation) − MISE(full) at βU=1.0\beta_U=1.0: None (0.148, 0.348), noOT (-0.049, 0.034), and noIPM (0.082, 0.203). Removing IPM worsens accuracy. OT is insignificant under weak U effect but gains as βU\beta_U increases, consistent with its role in debiasing hidden confounding.

[T1 vs T3 discrepancies] We apologize for the unclear details: Table3 reran full, noOT, noIPM, noJSR and None on a different set of 6 shared seeds for internally consistent ablation, hence the differences from Table1.

AuthorsOpenReview ↗

Response to EzEk comments of Questions

  • Q1[sensitivity to past S]: The JSR penalty trades off including more past S^\hat S as prediction inputs against propagating their bias (S^−S\hat S-S) along the sequence. JSR penalty does not force the learned dynamics to forget the past, but it may weaken dependence on earlier S. The Markov window δ\delta truncates/let model to forget only the history of S, while the long memory carried by Hˉt\bar H_t still enters the model. To examine the effects of δ\delta and JSR on tumour growth with true long memory, we added an experiment with true DGP windows δ⋆=5,7,15\delta^\star=5,7,15, βU=3.5\beta_U=3.5, T=15T=15 (full horizon), and fixed analysis window δ=4\delta=4. The 95% CIs for 3-seed paired MISE difference (noJSR-JSR): δ⋆=5\delta^\star=5: 0.088(0.033,0.142), δ⋆=7\delta^\star=7: 0.046(0.015,0.077), δ⋆=15\delta^\star=15: 0.011(0.007,0.016). Limiting sensitivity to past bias in earlier S predictions remains beneficial even under long-memory dynamics with a misspecified analysis window. Besides, Fig.2 & 3 also illustrate the trade-off with fixed δ⋆\delta^\star: more history improves prediction at first but hurts slightly beyond a certain point.
  • Q2[unclear writing]: We apologize for unclear writing and notation errors. The assumptions are intended to be identical in the main text and appendix; omitted intermediate steps brought confusion. We will improve writing structure and explanations, and clarify each component's purpose and the bias it addresses.

Thank you for considering these clarifications and additional results.

Reviewer_YMtrOpenReview ↗
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1
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3
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1
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Paper summary

This paper proposes a framework for long-term conditional average potential outcome prediction using longitudinal surrogates and data fusion under fixed time-varying treatments and unmeasured confounding. The method combines optimal transport-based reweighting, sequential surrogate prediction, autoregressive rollout, and balanced representation, with theoretical results concerning identification, distributional alignment, rollout error, and generalization error. The approach is evaluated on synthetic and semi-synthetic datasets.

Critical strengths
  • The paper addresses an important and challenging problem in longitudinal causal inference.
  • The proposed method outperformed the existing baselines with synthetic and semi-synthetic dataset.
  • The combination of longitudinal surrogacy and data fusion is a promising research direction.
Critical weaknesses
  • My main concern is the lack of precision in the problem formulation and mathematical development. Several key causal quantities, assumptions, and convergence statements are ambiguously or incorrectly formulated, making it difficult to verify whether the identification results, estimation procedure, and implementation are mathematically aligned.
  • The relationship between the prediction target and the evaluation metric (MISE) is unclear. Furthermore, Theorem 2 identifies the target through nested expectations over surrogate distributions, whereas the implementation appears to rely on deterministic autoregressive predictions. It is unclear whether the proposed estimator corresponds to the identification formula.
  • The experimental setting appears ambiguous. For example, the counterfactual treatment trajectories are not clearly defined in the MIMIC-III experiment. It is also questionable whether mean arterial pressure (MAP) alone is a sufficient surrogate for the effects of vasopressor treatment on 90-day mortality.
  • Although the paper claims to address dynamic treatments, it appears to consider only pre-specified fixed treatment regimes that do not depend on evolving patient histories.
Questions for authors
  • L130: Should the subscript tt in the dataset definition be TT, e.g., D0=[Aˉi,T,…]D_0 = [\bar{A}_{i,T}, \ldots]? The lengths of time horizons are the same in D0 and D1?
  • L134: What is the definition of Y(aˉt)Y(\bar{a}_t)?
  • L134: Under which distribution G=0 or G=1 the expectation is taken for the prediction target in Eq. (1)? Which t is the prediction target?
  • L131: Where the assumption n1≪n0n_1 \ll n_0 is used?
  • L142: What does "a given subject" mean in the consistency assumption?
  • L144: If AtA_t is continuous-valued, P(At=a∣…)=0P(A_t=a\mid\ldots)=0 except for at most countably many values of aa. Should the positivity assumption instead be formulated in terms of conditional densities or support?
  • L215: What target does the equation in Theorem 2 identify?
  • L226: Is P(G=0)/P(G=1)P(G=0)/P(G=1) identifiable from the sampling design or assumed to be known?
  • L249: Does ∇t\nabla_t depend on ν\nu?
  • L250: What is u^t\hat{u}_t?
  • L409: What is μi(a)\mu_i(a)? Is that different from the target μi,t(aˉt,hˉt)\mu_{i,t}(\bar{a}_t, \bar{h}_t) in Eq (1)?
1 comment
AuthorsOpenReview ↗

Responses to YMtr

Thank you for your comments. We apologize for the insufficiently polished presentation under time constraints, and will carefully revise the wording and structure to clarify the problem formulation, key notation, statement of assumptions and proofs, implementation details, and cross-sectional concept alignment. Specific corrections are given point-by-point below.

  • Q1: tt: timepoint of interest; TT: total time horizon collected for training, t<=T. D0,D1 may have different lengths T0,T1; we set T0=T1 for implementation.
  • Q2: Y(aˉt)Y(\bar a_t) is the potential long-term outcome (counterfactual) under treatment path aˉt\bar a_t, a classic causal inference notation, as in do(aˉt)do(\bar a_t), to emphasize intervention causality; other covariates are implicitly conditioned on.
  • Q3&Q7: The expectation is under the G=1 distribution for the unbiased prediction target, at any timepoint of interest t. Thm2 identifies Eq.1's unbiased conditional mean at time t: μ(aˉt,hˉt)=E[Yt(aˉt)∣Hˉt=hˉt,G=1]\mu(\bar a_t,\bar h_t)=E[Y_t(\bar a_t)\mid\bar H_t=\bar h_t,G=1].
  • Q4: n1≪n0n_1\ll n_0 is not an identification assumption; it reflects the problem setup: trials are much more expensive to collect than OBS data.
  • Q5: "a given subject": any individual i in the population. Consistency A1 can also be formulated as if Aˉit=aˉt\bar A_{it}=\bar a_t, then Sit=Sit(aˉt),Yit=Yit(aˉt)S_{it}=S_{it}(\bar a_t), Y_{it}=Y_{it}(\bar a_t) for any i,t.
  • Q6: We apologize for the imprecise wording. For continuous AA, positivity A2 requires conditional treatment densities on the target support, and debiasing should reweight by density ratios.
  • Q8: P(G=0)/P(G=1)P(G=0)/P(G=1) is identifiable from the observations and sample sizes n0,n1.
  • Q9: Yes. ν\nu is the (Rt,At)(R_t,A_t) marginal used in the integral.
  • Q10: Typo: appendix u^t\hat u_t should be w^t\hat w_t.
  • Q11: μi(a):μi,t(aˉi,t,hˉi,t)\mu_i(a): \mu_{i,t}(\bar a_{i,t},\bar h_{i,t}); we will clarify.
  • W2&W4[MISE and dynamic treatments]: We apologize for not clearly explaining dynamic treatments & MISE.

MISE integrated over Aˉt\bar A_t (implemented in Experiments): Following Yang et al. (2024b), we extend single-dose MISE to longitudinal dose-response. At each time, we randomly sample K possible ata_t from the assignment mechanism given patient history hˉt\bar h_t, then update hˉt′,t′>t\bar h_{t'},t'>t for future treatment sampling and surrogate prediction. Sequential Monte Carlo sampling thus forms K feasible dosing paths from the support A\mathcal A per subject. Averaging over sampled paths, not pre-specified fixed regimes, approximates ∫aˉt\int_{\bar a_t} under this history-dependent mechanism:MISE⁡^=1nTK∑i=1n∑t=1T∑k=1K[μ^(aˉi,t(k),hˉi,t(k))−μ(aˉi,t(k),hˉi,t(k))]2.\widehat{\operatorname{MISE}}=\frac 1 {nTK}\sum_{i=1}^{n}\sum_{t=1}^{T}\sum_{k=1}^{K}[\hat\mu(\bar a_{i,t}^{(k)},\bar h_{i,t}^{(k)})-\mu(\bar a_{i,t}^{(k)},\bar h_{i,t}^{(k)})]^2. MISE over the one AtA_t given history (alternative): at each time, fix hˉi,t\bar h_{i,t} (including prior doses), integrate over the current dose at∈Aa_t\in\mathcal A:MISE⁡=1nT∑i=1n∑t=1T∫A[μ^(at∣hˉi,t)−μ(at∣hˉi,t)]2 dat.\operatorname{MISE}=\frac{1}{nT}\sum_{i=1}^{n}\sum_{t=1}^{T}\int_{\mathcal A}[\hat\mu(a_t\mid\bar h_{i,t})-\mu(a_t\mid\bar h_{i,t})]^2\,da_t. Thm2 by definition corresponds to deterministic autoregressive predictions. For 2 timepoints with window width δ=1\delta=1, Thm2 identifies the target conditional on the covariate, treatment, and surrogate paths (the last truncated by Markov assumption): μ^(Aˉ2,Hˉ2)=h(Z2,A2,S^ˉ2)=h(Z2,A2,S^1,S^2)=h(Z2,A2,g(Z1,A1,S0),g(Z2,A2,S^1))=h(Z2,A2,g(Z1,A1,S0),g(Z2,A2,g(Z1,A1,S0))).\hat{\mu}(\bar{A}_2,\bar{H}_2)=h(Z_2,A_2,\bar{\hat S}_2)=h(Z_2,A_2,\hat S_1,\hat S_2)=h(Z_2,A_2,g(Z_1,A_1,S_0),g(Z_2,A_2,\hat S_1))=h(Z_2,A_2,g(Z_1,A_1,S_0),g(Z_2,A_2,g(Z_1,A_1,S_0))). Here g estimates the conditional E[St∣⋅]\mathbb{E}[S_t|\cdot] in each layer, so nested S^t\hat S_t plug-in is exactly the estimation counterpart of the nested expectations in the g-formula, i.e. the standard plug-in g-computation estimator, following the same rule as Longitudinal-S (Huang et al., 2026). This is not estimated over S prior distribution and reports Y posterior estimators as in Bayesian framework, which could be extended in future work.

  • W3[MIMIC-III counterfactual generation]: We generate Y recursively with δ=1\delta=1 from cumulative exposure and MAP: Yt=σ(β0+βL⊤Lˉt+βS(Sˉt−c)+βq(Sˉt−c)2+βmin⁡min⁡0≤j≤tSj),ℓt=log⁡St−SminSmax−St=a+ρℓt−1+αS⊤Lt+βcEmax(Ct)−βtoxHill⁡(Ct)+εℓ,t,St=Smin+(Smax−Smin)σ(ℓt)Y_t=\sigma(\beta_0+\beta_L^\top\bar L_t+\beta_S(\bar S_t-c)+\beta_q(\bar S_t-c)^2+\beta_{\min}\min_{0\le j\le t}S_j), \ell_t=\log\frac{S_t-S_{\text{min}}}{S_{\text{max}}-S_t}=a+\rho\ell_{t-1}+\alpha_S^\top L_t+\beta_c E_{\text{max}}(C_t)-\beta_{\text{tox}}\operatorname{Hill}(C_t)+\varepsilon_{\ell,t}, S_t=S_{\text{min}}+(S_{\text{max}}-S_{\text{min}})\sigma(\ell_t). The surrogate-model coefficients are fitted to real MAP trajectories. We will specify the counterfactual treatment-trajectory generation process in the appendix. [Why MAP as S]: The A-S-Y bridge scores are 0.0021 for lactate, 0.0011 for MAP, and 0.0001 for heart rate. Although its score is slightly lower than lactate's, MAP requires no invasive blood draw and is continuously available from an arterial line: within 24–30 h post-dose, patients have a median of 7 MAP readings vs 1 lactate result. Switching the surrogate to lactate worsens the 3-seed mean MISE by 0.019.

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