acceptodds
Withdrawn from ICLR 2027

ClinTic: Learning Clinical Dynamics through Treatment-Conditioned Neural SDEs

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

We propose ClinTic, a foundational model paradigm for ical trajectories built on a treatment-conditioned latent neural stochas differential equation (SDE). Patient state evolves continuously between sparse, irregular events with treatment as the driving action; ClinTic encodes multi-modal EHR streams into the SDE latent under Markov decision process (MDP)-aligned action conditioning, and per-step decoders read out clinically meaningful targets across the rollout. An IsoFLOP sweep over seven depths and six budgets ( to FLOPs) traces a clean Chinchilla-form frontier with size exponent , showing the paradigm is also scalable, with data more limiting than parameter count at this scale. ClinTic outperforms existing EHR foundation models and frontier LLMs across heterogeneous real-world cohorts, with the largest gain on a RECIST-PD-analogue cancer progression target (AUROC , over Opus-5). Risk representations read directly off ClinTic's dynamics separates 52-week OS where no standard biomarker reaches significance (HR overall, on Nivolumab); a further regimen-substitution probe on the same dynamics yields a stratifier of comparable discriminative power.

Primary area:
foundation or frontier models, including LLMs
Keywords:
foundation model, clinical dynamics, EHR, pathology, radiology

Reviews

Among:
Shape:
1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 5 reviews, above 0% of the others.
Reviewer_PCQ6OpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

This paper proposes CLINTIC, a treatment-conditioned latent neural SDE for modeling clinical trajectories. Multi-modal EHR events (assessment, imaging, pathology, treatment, genomics, and context) are encoded by modality-specific sub-encoders and a bidirectional Transformer with continuous-time RoPE into K readout latents, which are then rolled out with Euler–Maruyama integration conditioned on action tokens obtained by averaging treatment-event embeddings. The per-step decoder reads the latent before the action is applied, so that same-week treatment information does not leak into the prediction, and a JEPA loss with an EMA target encoder is used as an auxiliary objective. On MSK CCDE (oncology, weekly) and MIMIC-IV (ICU, hourly), the authors report better performance than existing counterfactual sequence models, EHR foundation models, and frontier LLMs. They further report a Chinchilla-form frontier with N*(C) ∝ C^0.25 from an IsoFLOP sweep, and claim that the progression probability read off the rollout stratifies 52-week survival, and that rollouts with a substituted regimen achieve comparable stratification.

Critical strengths

Timely problem setting. Moving EHR modeling away from static prediction of an outcome at a fixed time and toward modeling how patient state evolves under treatment as an intervention is a timely direction. It is a necessary step toward answering clinical questions that static predictors cannot address, such as regimen selection or whether a patient would meet a synthetic-control criterion.

Critical weaknesses

W1. The possibility that the performance gains come from the treatment actually administered during the prediction window is not ruled out

  • Treatment records in the prediction window can leak the outcome: CLINTIC's prediction at week t appears to be conditioned on the treatments actually administered within the dream window, a_0..a_{t-1} (Eq. 2, Figure 2, and the −action ablation). However, treatment switches, dose reductions, and discontinuations within this window are decided in response to the patient's course, such as disease progression or toxicity. Thus, even though the model does not directly receive observations from the dream window, the outcome enters indirectly through the treatment record. Eq. 2 only prevents same-week leakage, and the authors themselves acknowledge that drug-end events frequently encode progression (Section 3.6). In contrast, LogReg, XGBoost, and the LLM baselines only receive information prior to the prediction window (Appendix G), and it is not stated whether CRN and the other sequence baselines receive actions from the same window; even if they do, these are only binary indicators. Indeed, in the −action ablation, DiseaseChange AUROC drops from 0.827 to 0.738, close to the best baseline (0.712), suggesting that a substantial part of the +0.115 gain highlighted in the Abstract comes from this information. The same issue appears to apply to MIMIC-IV, where actions in hours 24–48, such as vasopressors and ventilation, are fed into the mortality and LOS predictions.
  • The prediction task is not clinically meaningful: For a treatment-conditioned prediction task to have clinical value, the treatment information given as input must be designed according to the clinical decision the prediction is meant to support. For example, if the goal is to support regimen selection, the input should be the candidate treatments available at the time of the decision. In contrast, information that this paper conditions on, such as discontinuation (drug-end events) decided in response to the patient's course, does not exist at the time the prediction is needed, and by the time it exists, the outcome is already known. In general world models, rollout fidelity can be evaluated with logged actions. In medicine, however, treatments are decided in response to changes in patient state in order to maintain it, so the treatment record itself is indicative of the outcome. In particular, since CLINTIC receives only treatments without any intermediate observations within the dream window, it can achieve high performance by reading the treatment record as a proxy for patient state without learning the dynamics. Therefore, directly transferring the world-model practice of evaluating rollouts under logged actions to the medical domain is not appropriate, and high performance in this setting does not indicate clinically usable predictive ability. This substantially weakens the authors' claims, which are motivated by clinical uses such as predicting the course under a different regimen or determining whether a patient meets a synthetic-control criterion (Section 1).

The authors should therefore (1) redesign the task according to the target clinical decision, using only treatment information available at prediction time, and verify in a clinical context that this input does not leak the outcome, and (2) compare models under conditions where all of them receive the same treatment information.


W2. The prognostic stratification and counterfactual rollout results do not support the claims

  • Insufficient comparators and reporting for prognostic stratification: s_13 is computed with the treatments actually administered in weeks 0–12 as input, so whether treatment was changed during this period already reflects prognosis. As the authors acknowledge, this is not a comparison against a multivariate survival model (Section 3.6); still, outperforming univariate biomarkers (PD-L1, EGFR, etc.) alone is not enough to support the claim that the representation learns prognostic information. The score should be compared against standard prognostic factors such as treatment change, baseline ECOG, stage, and line of therapy. In addition, only Nivolumab is reported at T=1, 4, and 13, with the highest value at T=13 (HR 6.35) used as the headline, whereas the other regimens are reported only at T=4 (Table 3). Results at the same landmark should be reported for every regimen.
  • Counterfactual rollouts without confounding control cannot be interpreted: Associations between treatment and outcome in observational EHR data are heavily confounded. For example, norepinephrine is mainly administered to patients with severe hypotension, so a model without confounding control may predict that administering it to a typical patient would substantially lower blood pressure. However, apart from conditioning on the history up to the baseline time, this study includes no explicit mechanism for confounding control (e.g., balancing, inverse probability weighting, or g-computation) and no check of identification assumptions such as positivity. In particular, because only treatments are fed into the dream window without intermediate observations, there is structurally no way to condition on the patient state that drove each treatment decision (time-varying confounding).
  • The presented results do not support counterfactual validity either: That the median-split HR is preserved under regimen-substituted scores only means that the risk ranking across patients is preserved; it is not evidence that the direction or magnitude of the treatment effect is correct. The authors note that these results should be read as diagnostic proxies for model coherence rather than causal effect estimates (Section 3.6), yet the Introduction presents answering counterfactual questions, such as the course under a different regimen, as a core motivation. The authors should either align the motivation in the Introduction with the scope of what is actually validated, or provide validation such as reproducing the direction of known RCT results.
Questions for authors

See weaknesses above

Reviewer_BEZhOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper introduces ClinTic, a framework for modeling clinical patient trajectories by combining multimodal event encoders, a treatment-conditioned latent neural stochastic differential equation (SDE), and a Joint-Embedding Predictive Architecture (JEPA) auxiliary loss. In this pipeline, heterogeneous clinical events (such as text notes, labs, vitals, and genomics) from an initial observation window are mapped into embeddings using small MLPs or ClinicalBERT and then encoded by a bidirectional Transformer with continuous-time rotary position embeddings into 16 latent readout tokens. From this initial state, a latent neural SDE rolls the trajectory forward over fixed time steps (weekly for oncology or hourly for ICU), conditioned on external treatment action tokens. At each step, small MLP decoders predict clinical targets, while an exponential-moving-average (EMA) target encoder and a JEPA predictor branch regularize the latent representations of future events without explicit decoding. The authors evaluate ClinTic on two cohorts: an oncology dataset (MSK CCDE, 23,320 patients) for predicting five weekly clinical assessments, and MIMIC-IV (68,546 ICU stays) for predicting 68 physiological channels, mortality, and length-of-stay. Beyond standard baseline comparisons against sequence models, EHR foundation models, and frontier LLMs, the paper also includes an IsoFLOP Chinchilla scaling-law analysis across model depths and compute budgets, as well as survival risk stratification and counterfactual treatment substitution experiments on the oncology cohort

Critical strengths

The authors attempt to build a new clinical foundation model framework that incorporates multiple different patient data modalities into a unified trajectory model.

Critical weaknesses
  • Unnatural paper flow and heavy LLM-style writing: After spending roughly an hour reading this manuscript, I found that the text feels heavily generated or over-polished by LLMs (even if the initial idea was not). Because of this LLM-generated style, the logical connections between different sections are weak and the overall flow of the paper feels very unnatural and hard to follow.
  • Disjointed combination of trendy techniques without clear motivation: This paper mixes together many different popular topics at once, including multimodal EHR encoding, neural SDE modeling, MDP action conditioning, JEPA representation learning, Chinchilla scaling laws, and counterfactual world models. However, putting all these blocks together lacks a clear core motivation. Even if such a complex foundation model exists, its practical clinical utility is unclear, and the paper does not convincingly explain what real-world problem this specific combination actually solves for clinicians or patients.
Questions for authors
  • The paper tries to pack too many different topics and technical elements into a single submission, which makes the work lack focus. If this paper is accepted, what is the main takeaway message the authors want to convey to the ICLR community? Are the authors suggesting that everyone should use neural SDEs combined with JEPA to model multimodal EHR data?
  • Several terms and abbreviations are used directly in the abstract and main text without clear definitions or context. Could the authors clearly define what "OS" (overall survival) and "last-write-wins" aggregation mean when they first appear, and explain why last-write-wins is a clinically appropriate choice for binning irregular medical events?
  • Are the authors the first to release the MSK CCDE dataset? If not, why is there no proper citation or public data link provided when MSK CCDE is introduced in Section 1 and Section 3.1 (unlike MIMIC-IV, which is properly cited)?
  • While I am not a scaling-law specialist, from my understanding, testing a relatively small model (around 8.2M non-embedding parameters) on a single 23,320-patient cohort up to 10^15 FLOPs is quite limited for claiming a general foundation model scaling law. Why is a Chinchilla scaling-law sweep a relevant or necessary topic in a clinical SDE paper, and how can two task-specifically trained cohorts support a general scaling claim?
  • In the introduction, the authors write: "CLINTIC wins all five MSK CCDE targets against 13 baselines and all three MIMIC-IV stay-level outcomes against CLMBR-T, ETHOS, EHRMamba (+0.066 AUROC, +0.189 AUPRC, +0.063 LOS accuracy)." For the second half of this sentence, it is unclear which specific baseline model CLINTIC is being compared against to get those exact delta improvements (+0.066, +0.189, +0.063), and why the text says "all three MIMIC-IV stay-level outcomes" when Table 4 only shows two tasks (Mortality with AUROC/AUPRC, and Length-of-Stay accuracy). Could the authors please clarify this?
Reviewer_HiMfOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The authors propose a framework for clinical trajectory modeling that incoporates both JEPA and a treatment-conditioned neural SDE. They apply their method to MIMIC-IV and MSK CCDE and provide evidence that the approach outperforms alternatives and has favorable scaling properties.

Critical strengths

I do not see any strengths.

Critical weaknesses

The authors do not motivate what they are doing or provide generalizable knowledge of value to the community. The methods section on the "treatment-conditioned neural SDE" (2.2), which is evidently the key contribution, is half a page of vague description devoid of context.

The writing is poor througout, with turns of phrase that may make sense to the authors, who already know what was done (though I tend to doubt even this); but which do not get the point across effectively to the reader, who is forced to repeatedly guess and second guess the authors' meaning while cross-referencing cryptic terms and phrasings.

"Each is bespoke per cohort and modality mixture, leaving no general framework whose continuous-time dynamics match the biology and whose ingestion absorbs heterogeneous EHRs without recipe-level rework" <- Here is one of countless examples. What does it mean for "ingestion" of continuous-time dynamics (or maybe the object is "world models"? It is not clear) to "absorb heterogeneous EHRs without recipe-level rework"?

Questions for authors

I don't have questions.

Reviewer_eiQLOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This papser sets out to generate patient trajectories conditioned on future actions (i.e. counterfactual trajectory generation). Naive past approaches solve forecasting tasks with a supervised model fitted on a fixed set of features. The problem is you want to model temporal structure and answer counterfactual future forecasts. Recent past works use world models to optimize policies for treating sepsis patients and perform counterfactual treatement-effect estimation using dataset, cohort, and task specific approaches. This work provides 4 contributions: (1) a general framework for multimodal clinical datasets that discretizes time (at the week or hour level for example) and uses an SDE in the generative model such that it has a continuous-time update of internal representations over time (its training loss is reconsruction loss plus a JEPA loss) (2) chinchilla scaling analysis: past work has shown chinichilla-form parameter-data scaling for next token prediction in the EHR setting, in this work estimates the scaling parameters for counterfactual estimation setting, (3) this work evaluates over two datasets, although the evaluations are completely different per dataset as will be discussed in more depth in the weaknesses section (4) this model provides useful patient-respresentations for downstream tasks.

Critical strengths

The paper proposes a multimodal generative model that uses event-level representations via mean-pooling modality representations in a time-bin. It additionally allows conditioning on actions or on placeholder unknown actions to support counterfactual generation, or non-counterfactual estimation. The results on the MSK dataset show it learns signals related to patient outcomes since the hazard ratio (between highest 50% predcited risk over lowest 50% predicted risk) is larger than 1, and the MIMIC results show improved performance on the chosen evaluations agains the current baseline models.

Critical weaknesses

Evaluation

Line 208: QWK is the evaluation metric for ordinal tasks ECOG and KPS, this is not a particularly interpretable metric. Could the authors additionally provide AUROC based on a few thresholds For ECOG what if you compute AUROC to compute discriminative performance of the methods between patients in ordinal classes: 0-3 vs 4-5 (Figure 2 shows the ordinal classes). Can it be shown that AUROC improvement is consistent across all 5 possible thresholds for ECOG. Can a sensitivity analysis like this be done for KPS as well, perhaps by quantiling up the KPS among patients and setting 4-5 threshholds from this and for each threshold comparing all models. I would like the authors to share what percent of these thresholds their method beats all other methods by a statistically significant amount.

For the AUROCs defined for DiseaseState and DiseaseChange tasks on Lines 209-210, what is yy what is "AUROC@(y≥2y\geq2)" for example. Is yy a task hyperparameter, and if so could a sensitivity analysis be performed over it? Additionally what is the motivation behind the current setting sused for those AUROCs? Can AUROC for each of the three classes be provided for Disease Activity?

For the baselines, why is ETHOS, Climbr-T, and EHRMamba not provided in Table 1 for counterfactual tasks. These model's can provide counterfactuals by inserting tokens during generation, or via rejection-sampling after generating many future trajectories.

Table 3 appears to be an evaluation of "evidence that the framework learns reprsentations carrying prognostic information" (Line 361) via evaluating the survival likelihoods from decoded future trajectories. This evaluation is performed by splitting patients into two equal sized groups based on sTs_T (the generative model's risk for the patient). It's confusing how s_T is derived from the model. Is it just the decoder probability from a single trajectory or from multiple trajectories at time bin T for Dchg being decoded to the progressing class?

The authors seperate patients into high risk and low risk subgroups based on likelihood DChg=Progressing from the generated trajectories. In the presented results they condition on ground truth future actions "The prediction at week T depends only on actions for weeks 0..T-1", however they point out that "treatment tokens leak into the prediction (drug-end events freqeuently encode progression)." and even claim that in another experiment where instead of using the direct risk at time T, and instead using the maximum risk across all 26 future time bins, that the large KM seperation between the highest risk patients and lowest risk patients "collapses... under a non-treatment ablation", and under a log-rank test the difference between the two subgroups drops from 8.8e-6 to 0.15, so the difference is not statistically significant between the subgroups the model predicts as high and low risk in a no leakage setting. The results for this ablation are not in the paper, and the results in table 3 still use this future leakage of actions where ground truth future actions from time 0 to T-1 are being used, strongly weakening the claim that these representations carry prognostic information in the typical non-dataleakage setting.

The counterfactual regimen subsitution evaluation shows that there still is non-trivial hazard ratios when we fix the actions to be a particular action token-type. It just shows that the patient outcomes under ground truth actions are correlated with the counterfactual risks predicted when we inject particular actions. This doesn't help to assess in a controlled manner if the the counterfactual action conditioning improves performance.

Line 415-416: what is meant by "in-domain ETHOS and EHRMamba, out-of-domain CLMBR-T-base. Can an AUROC be provided for Length of Stay with some threshold to binarize it? Are ETHOS, EHRMamba, and ClintTic used in a zero-shot manner to generate trajectories and compuate monte-carlo estimates for Mortaility and LOS? What is the time horizon used for the binary Mortality prediction task? This evaluation is a bit vague and the following need to be answered:

  1. How is the actual stay-level outcome computed. The final dream latent is generated stochastically for Clintic, so I am wondering if multiple forward passes are used and averaged or only a single is used?
  2. What treatment is provided as the action for Clinitic, I am concerned about data-leakage if ground truth future actions are provided during inference for only Clintic.
  3. ETHOS, EHRMamba, and CLIMBR-T are pretrained on next token prediction and can be used as zero-shot models, i.e. after pretraining they can generate future trajectories, and via Monte-Carlo sampling you can estimate patient risks for a task. Is this zero-shot inference being used here, or is each model being finetuned on each individual task after pretraining? If these results are zero-shot it is an unfair comparison with Clintic which has supervised training on the tasks of interest, and a more meaningful evaluation of generative performance would use the actually decoded trajectories (not the added supervised task heads).
  4. The compute comparison is not quantified when claiming ClinTic training on MIMIC is "achieved at lower end-to-end compute". Additionally there is a large inference cost as well, it may strengthen the paper to demonstrate an improvement in inference speed (trajectories/second for example).
  5. Why is there no evaluation on counterfactual tasks on MIMIC. This framework is designed to enable counterfactual analysis but there is no discussion of the action codes used for MIMIC-IV nor any counterfactual results.
  6. The approach should be evaluated (via AUROC) on a much more diverse variety of binary prediction tasks, not just Mortality and LOS on MIMIC.
Questions for authors

Note that I am unable to access the code for this submission because the code provided at the anonymous github link says "Unavailable", "This content can't be shown".

Please address questions in the weaknesses section. The evaluation needs quite a bit of work, one striking problem is that although results are presented on two datasets, the evaluations and baselines are very different between the two. I believe a much simpler presentation is one where the authors have the same set of baselines for both datasets and look at the same two evaluations for both, one is the common zero-shot evaluation, generate future trajectories (no access to future conditions) and see how generative performance compares for particular downstream tasks. Then do a conditioned evaluation where at particular time points where you know an action would occur you condition on it and see if that helps.

For the ISOFLOP comparison, the contribution claim in Line 053 (continued on line 081) "scales predictibly with data breath" is not supported by the ISOFLOP comparison since that trades off parameter count (model size) for the number of training tokens processed. The number of training tokens processed is not equivalent to data breath seen by the model. For example, assuming a fixed number of training tokens are trained on, let's say it's 1 million, if dataset A has 1,000 tokens and dataset B has 1 million tokens, dataset A only sees 1,000 unique tokens but is trained for 1,000 epochs, while dataset B is only trained for 1 epoch, so the same number of flops are used if we have the same model architecture but the data breath is different. A seperate comparison analyzing number of unique patients seen during training (instad of flops) for example, or number of unique tokens would be needed for a data breath scaling claim.

The authors provide ablations of JEPA, SDE, and action. The ablations show a very modest loss of performance in AUROC when ablating JEPA and SDE, could the authors provide Table 2 with an AUROC only variant and with condfidence intervals in the table, and only bold when the difference is statistically significant.

Clarity:

Could a citation be provied for the dataset "MSK CCDE" if it is public. Only an acronym is provided and I could find no corresponding public dataset online. I don't believe the manuscript currently specifies whether this dataset is public or private.

Line 104: It is unclear what the eie_i, Encτi(rawi)\text{Enc}_{\tau_i}(\text{raw}_i), and Wmod[τi]W_\text{mod}[\tau_i]. Is ii indexing single modlity specific observations, or events? What is channel routing in line 105. It would help to clarify which parts are at the modality embedding portion of the architecture and which are at the event encoder part, and potentially seperating indexing for events vs the the particular modality observations within an event.

Line l05: What is "channel routing" and how does "Wmod[τi]W_\text{mod}[\tau_i] tag preserve[s] channel routing" Line 115: rr is not defined

Line 125 wording is a bit ambigruous as well in regard to whether mean pooling is inter-event or intra-event.

The acronymn HR (which I think is hazard ratio) is mentioned many times in the paper, but is never defined.

What is "n / ev." column in table 3 Line 345? Is it total number of samples at risk in the bin / number that experience the event in the bin.

How is the placeholder action token trained. During trianing are ground truth future actions always used or are these placeholders always used or is there some rule for sampling when to use one or the other? It does not appear that this is explained in the manuscript.

It should be clarified how the authors compute the hazard ratio given KM curves. There are different approaches one can use so it should be specified.

Nits

  • Line 035: "models cast this", it is unclear what problem this refers to. Is it general forecasting tasks?

  • Line 086: Define dream-window before using it

  • Line 085-089: This last part of the introduction is challenging to read on a first pass since acronyms for tasks such as HR, OS, NSCLC and other terms such as dream-window are used without context. I would recommend a simpler highlight of biggest improvement on a single task or average improvement across tasks, and define the dream-window before mentioning it or just explain use a generally understandable term that does not require generalization here.

  • Equation (2): traj[t] is defined and then never used again.

  • Please bold Opus-5 for DST task in Table 1 since it also is a column max.

Reviewer_uzWLOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper presents ClinTic, a foundation model for clinical data. It consists of feeding known encoders into a latent dynamics SDE and performing predictions via SDE rollouts rather than making discrete predictions directly. They also add a JEPA head/loss to fix how clinical trajectories are often underdetermined.

Critical strengths

The idea is sensible, and the implementation appears sound.

Critical weaknesses

Much of the work is motivated by evaluating patient outcomes under counterfactual trajectories. However, there is no form of rigorous confounding adjustment within ClinTic, nor are there experiments to support empirically whether ClinTic implicitly learns to adjust for confounding. Although, to their credit, the authors acknowledge this directly (Line 132), the utility of unadjusted rollouts is not clear. The literature on causal inference contains straightforward estimators that can be directly folded into this framework (e.g., AIPW when evaluating under a counterfactual action) to then pass latent dynamics into the SDE that can more rigorously claim to determine the causal effect in question. To test, the authors could then generate synthetic data with known counterfactuals (e.g., using an established clinical data simulator like https://github.com/synthetichealth/synthea), vary the degree of confounding manually, and comparing rollout error on the counterfactuals. I'd be interested to see this experiment performed both with and without the inclusion of a formal causal estimator, to see if ClinTic implicitly learns confounding adjustment. If so, that could be a very noteworthy result, especially if it learns to adjust for confounding better than baseline approaches (maybe the learning signal from rollouts is better at confounding adjustment than from a discrete classification approach).

The scaling laws seem unnecessary at this low-scale. In these clinical settings, data is almost always the limiting factor, rather than parameters or compute.

Utility of the cross-cohort validation is overstated. The authors acknowledge it's an apples-to-oranges comparison since their method is trained on the target cohort while the baselines aren't. The biggest issue with this is, as far as I can tell, that's their primary comparison to the established clinical foundation model baselines. Lacking other and more thorough comparisons, it's hard to tell whether this SDE-based approach works well in practice or if the reported performance improvements are merely the result of fitting on the same dataset as evaluation is being conducted on, and not affording the baseline models that same luxury.

Questions for authors

Has this paradigm of prediction from rollouts been seen in other domains? I can see why it might make sense for clinical domains, but are there links we should be drawing to, e.g., robotics or other fields? That would be super informative, as it could tell me if this is a natural / successful approach in other areas that we're adopting for the clinic.

Table 1 is unsurprising. The authors compare a hugely powerful, massively parameterized, multimodal model against mostly simple baselines (plus Claude). Can the authors construct a set of baselines (simple + clinical/multimodal) that are consistent across all experiments? The shift between baselines in Table 1 and Table 4 is striking, and it's unclear why this is so inconsistent.

Can the authors come up with a better apples-to-apples comparison against the larger clinical baselines?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Discussion (0)

Sign in to comment.