acceptodds
Under review as a conference paper at ICLR 2027

Bridging Longitudinal Health Records and 3D Human Generators with Biomarker-Guided Signed Choquet Forecasting

Abstract

Longitudinal health records contain compact, structured measurements, while pretrained 3D human generators operate on high-dimensional visual conditions. We study how to connect these representations when the health cohort has no participant-specific 3D scans. We introduce the Signed Choquet Twin (SCT), a health digital twin that forecasts body and blood measurements from diet records and turns those forecasts into 3D bodies. SCT predicts each person's expected change from their age, sex and baseline measurements, then adds a diet term built from the 11 components of the Alternative Healthy Eating Index. This term uses a symmetric Choquet integral that assigns a weight to each component and to each pair of components, so every forecast breaks down exactly into the contributions of individual foods and their interactions. A key result is that this diet term is linear in its weights, and the valid weights form two convex cones, which makes estimation clean and exact. Cross-fitted networks first remove the influence of each person's background, and small convex quadratic programs then give the exact weights, with cross-validated shrinkage toward the total diet score. To generate bodies without real scans, SCT learns from generated reference bodies how changes in measurements should shift the input to a frozen image-to-3D generator. On 7,876 participants from two long-running studies, SCT forecasts ten measurements more accurately than regression, gradient boosting and a Choquet baseline. These accuracy gains come from the trajectory networks, while the diet term contributes interpretability. Better diet quality is consistently linked to lower body weight and a smaller waist across all training runs. The total diet score captures most of this effect, and a synthetic cohort with known effects confirms that the model recovers the overall diet effect reliably. The 3D trajectories remain qualitative because measured longitudinal 3D scans are unavailable, so we present SCT as a measurable pipeline from longitudinal health records to explainable diet effects and 3D visualizations, together with a practical route for generating temporal body updates without paired 3D supervision.

Primary area:
interpretability and explainable AI
Keywords:
longitudinal health records, 3D human generation, Choquet integral, biomarker prediction, latent conditioning, low-rank adaptation, longitudinal modeling

Reviews

Among:
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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_A5LiOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper focuses on the signed Choquet twin (SCT), which forecasts body and blood measurements from longitudinal diet records of 7876 participants. The method can render the results as a 3D body without any scans. Each outcome's change is modeled as a diet-free trajectory network and a diet term built from a symmetric Choquet integral with 2 additional components. The 3D path learns a ridge map from 7 body features to the conditioning space of a frozen generator using 320 synthetic reference bodies. SCT achieved the most accurate performance.

Critical strengths
  1. The analysis shows the diet effect is estimated accurately and stably; the authors show the diet model as a simple linear problem with 66 weights. As a result, the sign of the overall diet effect is the same in 25 runs, proving that the method is accurate.
  2. The framing of the problem is innovative, such as the debiased cross-fitting and Neyman orthogonality in the learning, so the neural trajectory networks absorb the confounding effect.
  3. The experiment design and ablation studies are robust and comprehensive.
Critical weaknesses
  1. The effectiveness and accuracy gains are marginal; more highlighting of the novelties is needed. Or more analysis of the gains from generic trajectory networks or other perspectives.
  2. The cohort disbution need more clarity, looks like 9/10 outcomes are from senior women, more cohort representativeness can be described.
  3. The diet signal itserlf is weak and might need stability analysis.
Questions for authors
  1. Cross-validation picks report timing in 19/25 runs, so most forecasts use diet reported at the target visit. For a twin to answer "what if I change my diet?", only start timing seems valid. Under start timing alone, do the whole-cohort effects for weight, waist, insulin, and HOMA-IR still exclude zero?
  2. No baseline trains one network end-to-end on context, baseline outcomes, time, and diet history. What skill does it reach? If it matches 0.249, then the accuracy claim reduces to "an MLP beats ridge and boosting," and the abstract should say so.
  3. Nine outcomes come only from older women (Study B) and HOMA-IR only from young adults (Study A), with sex confounded with age band and era. Do the diet effects hold when each study is fit separately?
  4. The synthetic study shows single-component intervals cover only 33% of true effects at κ = 0.3, the anchor chosen on the real cohort. Will it either report real-cohort component effects at κ = 0 with valid intervals, or drop the component-level claims (e.g., the trans-fat/fruit/nuts ordering for weight)?
2 comments
AuthorsOpenReview ↗

response to reviewer A5Li: Part 1

Thank you for a sharp and concrete review. Each of your questions was a clear test, and we ran all of them. Some answers support the paper and one confirms your suspicion. We report both in the revised paper.

Question 2: what does an end-to-end network reach?

We ran exactly this baseline (Table 1, Appendix F). It uses the same architecture as our outcome networks, five seeds on each of the same five participant splits, and settings chosen by validation skill.

Its inputs are context, baseline measurements, time and longitudinal diet features. These are the running averages of the component scores under both timing conventions, the baseline component scores, and the component scores and their total at the scored visit. The first version called these inputs "diet history". One of the source studies uses "Diet History" as the name of its diet questionnaire, and we do not mean that plainly, so the revised paper now uses "longitudinal diet features".

  • With the diet features, the network reaches a skill of 0.239, against 0.249 for our model. Using unrounded values, the paired difference is 0.011, with a 95% interval from 0.006 to 0.015.
  • Without any diet input, the same network reaches 0.246. Its difference from our model is 0.003, with an interval from -0.002 to 0.008, so the two cannot be told apart.

This supports your point: the gain in accuracy over the classical baselines comes mainly from modelling the trajectory with a neural network. We now say this in the abstract and the introduction.

What our model adds is a more consistent diet estimate. For a diet one standard deviation better, the estimated weight associations are:

ModelAverage over runsStandard deviation across runsRuns with a positive estimate
End-to-end network-0.86 kg0.64 kg5 of 25
End-to-end network with pair features-1.03 kg1.34 kg6 of 25
Our model-1.05 kg0.34 kg0 of 25

Our model also splits the diet contribution exactly into component terms and pair terms. This split is a mathematical property. It does not show that the cohort supports each component or pair on its own.

Weakness 1: the gains are marginal; highlight the novelty.

We revised the abstract and the introduction so that they lead with the estimator, not with accuracy.

What is new technically:

  • Proposition 1 shows that the valid coefficients of the signed 2-additive Choquet diet term form the union of two convex polyhedral cones.
  • After we adjust both the outcomes and the diet features for context and time with cross-fitting, the fit reduces to two small convex quadratic programs.
  • Solving both and keeping the better one gives the global optimum of the diet objective, given the fitted adjustment networks and the selected settings.
  • The diet contribution splits exactly into component terms and pair terms.

In practice (Tables 2 and 4):

  • The weight association of our model is negative in all 25 runs.
  • Without the capacity constraints, the estimate is positive in 20 of 25 runs.
  • For the end-to-end network, it is positive in 5 of 25 runs.
  • On synthetic data, where the true effect is known, our model recovers the overall planted effect in seven of eight outcomes and it overestimates the effect for insulin.

One clarification on the gradient-descent comparison: Appendix D shows that gradient descent run to convergence on the same objective reaches the same solution as the exact solver. The larger differences in the staged gradient baseline also come from its training order and its parameterization, so we do not credit all of that difference to the exact solver.

Our model is ahead of ridge regression by 0.022 (95% interval 0.016 to 0.029), the linear mixed model by 0.023 (0.016 to 0.031), and the explainable boosting machine with pairs by 0.012 (0.006 to 0.019). It is comparable to the neural network without diet. So what we emphasize is a constrained and interpretable diet estimate, together with competitive prediction.

Question 1: with start timing only, do the effects still exclude zero?

Yes for weight, waist and insulin. We repeated the whole-cohort analysis using only diet reported before each outcome visit, with the settings chosen within start timing (Table 3). For a diet one standard deviation better, the adjusted associations are:

OutcomeEstimated changeApproximate 95% interval
Weight-1.08 kg-1.76 to -0.52
Waist-0.99 cm-1.59 to -0.47
Insulin-0.88 micro-units per mL-1.68 to -0.31
Insulin resistance (HOMA-IR)-0.31-0.60 to +0.01

The estimate for insulin resistance is still negative, but its interval just includes zero, so we call that evidence inconclusive at the 95% level. Skill is essentially unchanged (0.2488 against 0.2490).

Start timing keeps the order in time right and the main associations remain. The study is still observational, so we do not read these numbers as the effect of an intervention.

AuthorsOpenReview ↗

Response to Reviewer A5Li: Part 2

Weakness 2 and Question 3: who is in the cohort, and do the effects hold in each study separately?

We made the make-up of the cohort clear and added fully separate analyses for each study.

Follow-up measurements for nine outcomes come from Study B, which enrols women aged 50 to 79. Insulin resistance comes from Study A, which enrols men and women aged 17 to 35. So each outcome's association was already informed by follow-up data from one study. What the pooled analysis shared was the adjustment networks, the diet standardization and the settings.

To test whether pooling mattered, we refitted the networks, the standardization and the settings on each study alone, with 50 new cross-fitted runs (Table 13).

StudyOutcomeEstimated association95% interval
BWeight-1.10 kg-1.65 to -0.71
BWaist-1.09 cm-1.59 to -0.76
BInsulin-0.72 micro-units per mL-1.45 to -0.35
AInsulin resistance (HOMA-IR)-0.36-0.61 to -0.20

The main associations remain when each study is fitted on its own. The intervals for systolic and diastolic blood pressure also exclude zero in the Study B refit. This shows that the findings do not depend on pooling. It is not a replication of the same outcome in two populations.

Table 9 now reports, for each study, the demographics, baseline years, follow-up schedule, number of participants left at each visit, share of imputed diet records, and baseline missingness. The abstract and the discussion say which population each estimate refers to. Age band and sex cannot be separated from study in this design, so we make no claim about differences by age or sex.

Weakness 3: the diet signal is weak; is it stable?

We agree that these are two different questions: how much diet adds to prediction, and how stable the association is. The diet term adds little accuracy on this cohort. The main associations, however, hold across the following checks (Appendices C and G).

  • Diet imputation. Fitting each of the five imputations separately and combining them with Rubin's rules gives a weight association of -1.25 kg (95% interval -2.03 to -0.48), negative in all five. We also repeated this with ten imputed diet datasets: -1.29 kg (-2.10 to -0.47), negative in all ten. With ten imputations, the intervals for waist, insulin and insulin resistance also exclude zero.
  • Subsets of participants. We refitted 20 times on half of the participants and 20 times on three quarters. The weight association stayed negative in all 40 refits. Its interval excluded zero in 14 of the 20 half-size refits and in 18 of the 20 three-quarter refits, as expected when smaller samples give less precision.
  • New folds and retrained networks. Redrawing the cross-fitting folds and retraining the networks gives a standard error for weight that is 0.97 times the one from the fixed-network analysis. For insulin resistance the uncertainty grows more, by a factor of 1.49, although its interval still excludes zero.
  • Earlier evidence. The direction is the same in all 25 split runs, the overall association depends only modestly on the anchor, and height, our negative control, shows no detectable association with diet.

Stability is not the same as robustness to confounding, so we report that separately. The approximate E-values for weight are 1.63 for the estimate and 1.46 for the interval bound nearest zero. This means that unmeasured confounding of moderate strength could explain the association away. These checks do not make the result causal, and we keep reading it as an adjusted association.

Question 4: report component effects with valid intervals or drop the component claims?

We did both.

  • We removed the ranking of components from the main text.
  • We added a separate analysis in Table 14. For weight, waist, insulin and insulin resistance, it reports the component estimates from an additive fit without constraints, their participant-clustered 95% intervals, and p-values with a Holm correction across the 11 components within each outcome.

No component remains significant after the correction. The smallest adjusted p-value is 0.07, for trans fat and weight.

We also looked at the cone-constrained fit with no anchor, as you suggested. In its bootstrap, many refits put a component exactly at the edge of the cone. So even where an interval appears to exclude zero, we do not use it as ordinary evidence for that component. The rankings that remain in the appendix are marked as exploratory and carry the coverage warning from the synthetic experiments.

Our revised conclusion separates the two things. The model splits the diet contribution exactly, which is a mathematical property. On this cohort, the data do not establish associations for single components beyond an equal-weight diet score.

Thank you again. Your questions led directly to the strongest new evidence in the revision.

Reviewer_2fnSOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The authors introduce the signed Choquet twin (SCT), a model that forecasts health measurements from diet records and turns the predictions into 3D visualizations. SCT models each outcome as the expected change from characteristics such as age, sex, and the baseline measurements, plus a diet term. The diet term uses a symmetric Choquet integral which assigns a weight to each component and each pair of components, and the diet term is shown to be linear in its weights with the valid weights forming two convex cones (mirror images) so estimation reduces to partial linear regression. On evaluation, SCT outperforms baselines such as regression, gradient boosting, and a Choquet baseline. The 3D visualizations are presented as qualitative results and evaluated by comparing the mass-implied volume change with the volume change of the visualized 3D body, revealing the agreement quantitatively.

Critical strengths
  1. The authors decompose the diet forecasting problem into an elegant, interpretable model with a clear and separate baseline component, a diet-free trajectory, and a diet term (a symmetric Choquet integral with a 2-additive capacity over centered diet components).
  2. The mathematical exposition of the model is especially clearly presented and easy to follow. The reviewer also appreciates the proofs in the Appendix.

Overall reasons to accept outweigh reasons to reject.

Critical weaknesses
  1. The paper does not report confidence intervals, especially for main results such as in Table 1 and Table 2 and thus lacks any evidence of statistical significance of the difference in performance numbers. The reviewer would appreciate the inclusion of CIs or justification of the lack thereof.
  2. Overall, the bridge between longitudinal health records and 3D visualization seems to be insufficiently motivated. As it stands, the modeling for body and blood measurements and the 3D visualizations from the forecasts seem to be disparate parts of the research, with the latter only motivated in passing in the Introduction, “A visualized future body can convey risk more directly ...”. Some elaboration or contextualization for the 3D bodies aspect would strengthen the narrative of the paper.
Questions for authors
  1. Could the authors provide justification for the imputation to 0 for missing values for the baseline outcomes? Section 3.1 mentions both the imputation, and also that the missing values are “flagged”, so it would be useful to know how the flag is utilized.
  2. Could the authors provide details for the process to determine which baselines to include in the performance comparison? The reviewer would be interested to learn if other classes of models were considered which may also be suitable for this modeling problem, as the baseline comparison cohort seems a bit limited.
3 comments
AuthorsOpenReview ↗

Response to reviewer 2fnS: Part 1

Thank you for the positive and helpful review. We especially appreciate your comments on how clearly the model is decomposed and on the proofs. We have addressed all four of your points with new experiments and text and we answer each one below.

Weakness 1: no confidence intervals for Tables 1 and 2.

We agree this was missing. Table 11 now gives a 95% interval for every difference in skill, from a paired bootstrap over participants:

  • we resample test participants 1000 times, always keeping all visits and all imputed records of a person together;
  • on each resample we recompute the overall skill of both models;
  • we report the interval of the difference between them.

We did this in two ways. The first averages over the five test splits. The second uses cross-fitted forecasts, where each participant is predicted exactly once by models that were trained without that participant. The second way avoids the overlap between the five test sets. The two agree.

Our model compared withFive splits: difference in skill (95% interval)Cross-fitted: difference in skill (95% interval)
Ridge regression0.022 (0.016 to 0.029)0.022 (0.016 to 0.028)
Linear mixed model0.023 (0.016 to 0.031)0.018 (0.011 to 0.025)
Gradient boosting0.053 (0.042 to 0.065)0.044 (0.033 to 0.054)
Explainable boosting machine with pairs0.012 (0.006 to 0.019)0.010 (0.003 to 0.016)
Neural network without diet0.003 (-0.002 to 0.008)-0.0004 (-0.0042 to 0.0028)
  • Our model is ahead of the four classical baselines and each of those intervals excludes zero.
  • Against a neural network that sees no diet at all, the difference cannot be told apart from zero.

So we now say plainly that the gain in accuracy comes mainly from modelling the trajectory with a neural network, not from the diet term. Table 2 gives the same kind of interval for the diet-term ablations: for the full model, the start-timing variant and the equal-weight variant, adding diet gives no detectable gain in accuracy.

One note on what these intervals mean. They describe how the comparison would vary with a different set of test participants, for the models as fitted. They do not cover every source of variation in training.

Weakness 2: the 3D part is not well motivated.

We rewrote this part of the introduction so that the practical reason, the technical gap and the evaluation follow from one another.

  • Why bodies. A picture of a body is a visual companion to a table of numbers. This is motivated by work on visual aids in risk communication (Garcia-Retamero and Cokely, 2013) and on virtual self-representations (Fox and Bailenson, 2009).
  • The gap. Body models trained on 3D scans exist, but this cohort has no scans of its participants. Our task is to turn recorded and predicted body measurements into 3D geometry in that situation. For a visualization grounded in measurements, we do not need the real face or appearance of a person.
  • Why join the two parts. The forecaster produces height, weight and waist, which are the inputs the bridge needs. Joining them lets us evaluate the whole path, from longitudinal records to body geometry.

We also report what the evaluation shows, including where it is weak.

  • Controlled edits behave as expected. Adding 8 kg increases body volume in 47 of 48 body and seed pairs, and removing 8 kg decreases it in 47 of 48.
  • Changes driven by the forecast are subtler. Among the 16 participants with a measured follow-up, predicted weight changes vary across people with a standard deviation of 2.5%, while the measured changes vary with 6.5%.
  • Separately, the generator itself varies from seed to seed: the median change in volume between seeds is 3.1%.

These are two different sources of variation, one from the forecast and one from the generator, and we now evaluate both. Together they explain why small changes are hard to read from the rendered bodies. What we claim is a tested bridge for visualization. We do not claim a proven benefit for patient communication, and we do not claim to reconstruct what a particular person will look like.

AuthorsOpenReview ↗

Response to Reviewer 2fnS: Part 2

Question 1: why fill missing baseline values with zero, and how is the flag used?

  • Each baseline measurement is first standardized using the observed training values. After that step, zero is the training mean, so filling a missing value with zero is mean imputation. It does not mean a physical value of zero.
  • Each of the ten baseline measurements comes with a yes-or-no missingness indicator, and both go into the networks. The indicator lets the networks tell a missing value apart from a measured value that happens to be near the mean, and lets them use the other inputs differently when a value was not measured.
  • Some of the missingness is by design. Study B has no insulin resistance (HOMA-IR) measurements at all.
  • Missing outcome values are handled separately. They are never filled in; they are left out of the training loss and out of the evaluation.

Section 3.1 and Table 9 now make this distinction clear. Apart from the by-design gap, baseline missingness is at most 4.3%.

We ran two sensitivity checks.

First, the baseline measurements. We replaced mean imputation with nearest-neighbour imputation, using ten neighbours and fitting it on training participants only, and we kept the indicators. We retrained all 25 runs. Skill stayed at 0.249. The average weight association moved from -1.05 to -1.06 kg and stayed negative in every run. So the findings do not depend on which of these two ways we use to fill in baseline values.

Second, the diet scores, which are the other place where values are filled in. The paper uses five imputed diet datasets. We repeated the analysis with ten imputed diet datasets and retrained all 25 runs.

  • Skill stayed at 0.249.
  • The average weight association across the runs was -1.08 kg, against -1.05 kg with five imputations, and it was negative in all 25 runs.
  • Fitting each of the ten imputations separately and combining them with Rubin's rules gives:
OutcomeTen imputations (95% interval)Negative in
Weight-1.29 kg (-2.10 to -0.47)10 of 10
Waist-1.27 cm (-1.91 to -0.63)10 of 10
Insulin-1.05 micro-units per mL (-1.99 to -0.12)10 of 10
Insulin resistance (HOMA-IR)-0.45 (-0.69 to -0.21)10 of 10

For comparison, weight with five imputations was -1.25 kg (-2.03 to -0.48). The estimates and the widths of the intervals are almost the same with five and with ten. Using more imputations makes the combined estimate depend less on the random draws. It does not remove the uncertainty that comes from the diet values being missing in the first place, and these intervals already include that uncertainty. This check is now in Appendix G.

Question 2: how were the baselines chosen, and were other model classes considered?

The original baselines were chosen to cover:

  • simple references: no change, and a linear trend;
  • regularized linear prediction: ridge regression;
  • nonlinear learning on tabular data: gradient boosting;
  • an earlier Choquet-based model.

With at most four visits per person, we gave priority to models that suit sparse longitudinal records.

Following your suggestion, we added three more classes (Table 1 and Appendix F):

  • A linear mixed model with a random intercept and a random slope for each person. This is a standard approach for longitudinal data. Skill 0.226.
  • An explainable boosting machine with ten pairwise interactions. Skill 0.237.
  • A neural network trained end to end, with skill 0.239, and the same network without any diet input, with skill 0.246.

Our model reaches 0.249.

The end-to-end network receives context, baseline measurements, time, and what we call longitudinal diet features. These are the running averages of the component scores under both timing conventions, the baseline component scores, and the component scores and their total at the scored visit. The first version called these inputs "diet history". One of the source studies uses "Diet History" as the name of its diet questionnaire, and we do not mean that instrument, so the revised paper now calls them "longitudinal diet features" throughout.

All models use the same participant splits. The mixed model predicts the random effects of test participants from their baseline information. For the explainable boosting machine, early stopping holds out whole participants, with all their visits and imputed copies, so that nothing leaks between training and validation.

The comparisons under report timing include diet reported at the same visit as the outcome. The start-timing analyses separately look at associations that use earlier reports only.

In short, these comparisons show that our model predicts as well as the strongest alternatives and gives a more consistent estimate of the dietary association. We do not claim that it is more accurate than the neural network without diet.

Thank you again for your support and suggestions. They made the paper's evidence much stronger.

Reviewer_2fnSOpenReview ↗

Response to Rebuttal

The reviewer appreciates the thorough response from the authors. The narrative of the paper is now stronger, and the comparisons more thorough and transparent. Thus, the reviewer would like to increase the score from 3: Weak acceptance to 4: Clear acceptance

Reviewer_mz2EOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper proposes a model based on the symmetric Choquet integral that forecasts longitudinal changes in body and blood measurements from diet records and renders the forecasts as 3D bodies with a frozen image-to-3D generator, without participant scans. Each forecast combines the trajectory expected from the participant’s baseline characteristics (age, sex, and baseline measurements) with a diet term that captures deviations from the diet typical of that background. The main contributions are: (i) a diet term built on a symmetric, 2-additive Choquet integral, which is linear in its weights; following this formulation, the valid weights form two convex polyhedral cones, so they can be estimated exactly by convex quadratic programming; (ii) a scan-free bridge that maps the forecast outcomes to 3D bodies through a frozen image-to-3D generator; and (iii) an evaluation on 7,876 participants from two longitudinal cohorts. The proposed model outperforms all baselines in forecast skill, but the gain comes from the context networks that model the diet-free trajectory rather than from the diet term. The diet term yields a stable association between better diet and lower weight, waist, insulin and HOMA-IR, with little evidence that individual components or pairs matter beyond the total score. Synthetic experiments recover the overall diet effect well but pairwise interactions poorly. Regarding the renderer, the authors present the 3D results as qualitative: only large weight edits produce consistent changes, with realistic forecast changes falling below the generator’s seed-to-seed variability.

Critical strengths

To my knowledge, this is the first work to embed a constrained Choquet capacity in a diet forecasting model. The key observation is that the set of all products of an effect size and a 2-additive capacity forms two convex polyhedral cones. The diet weights are therefore obtained as the exact solution of a convex program rather than by gradient descent. The exposure and outcome networks account for each participant’s background, modelling how both the outcomes and the diet depend on age, sex, and baseline measurements, so that the diet effect can be estimated separately from the expected trajectory. This offers a reusable recipe for combining flexible predictors with structured, interpretable effect estimates, relevant beyond diet to other longitudinal health twins. The authors test every component of the fit through ablations, compare against carry-forward, ridge, boosting and a Choquet baseline on identical splits, and validate on a synthetic cohort with known effects. They also report negative results openly: the diet term adds no accuracy, component weights are not shown to matter beyond the total score, planted pairs are poorly recovered, and the 3D forecasts fall below the generator’s noise. This is consequential because it makes the paper’s claims verifiable and well bounded, and it gives a reliable picture of what the method can and cannot deliver.

Critical weaknesses

The paper is very dense, and essential information is scattered or left implicit. The exposition makes the method hard to follow and obscures its contribution. A substantial rewrite would be needed for the contribution to be more accessible. Moreover, the paper presents the proposed framework as a digital twin, but the evidence does not support that use. The forecasting accuracy comes from the context networks that model the diet-free trajectory rather than the diet term, and the diet effects are not shown to matter beyond the total score. This is consequential because the digital twin framing is the paper’s main motivation. Without evidence that the tool provides reliable, actionable individual “what-if” predictions or visualizations, the contribution reduces to an interpretable re-estimation of an association already captured by the total diet score.

Questions for authors
  1. Appendix A shows that the loss is stationary in the nuisances at the true parameters. Neyman orthogonality, however, requires the score ∂L/∂θ to be insensitive to the nuisances, and stationarity of the loss does not imply this. For example, L = (θ − θ₀)² + η(θ − θ₀) satisfies the stated condition, while argmin θ moves linearly in η. Nevertheless, the property does hold for this partially linear model. I suggest that the authors correct the proof by showing that the score ∂L/∂θ has zero derivative with respect to ℓ and e at the true values, using E[φ − e | w] = 0 and E[ε | w] = 0.
  2. The validity of the reported intervals (Appendix B, Table 3) is unclear, since both the second-order robustness claim and the bootstrap intervals rely on results that hold for unconstrained, unpenalized estimators. The estimator of eq. 5 is different, because it is constrained to K ∪ (−K), L1-penalized, and anchored with a cross-validated κ. In addition, the bootstrap holds the nuisance networks and the selected settings fixed. I suggest that the authors state explicitly which results come with valid inference (most likely the overall diet effect and the total-score test) and which do not (component and pair intervals). Moreover, given the authors’ own synthetic results (33% coverage for single components at κ = 0.3, Table 12), are the component- and pair-level intervals meant to support any of the paper’s claims?
  3. Membership in K forces all 11 component weights to share the sign of the effect (or be zero), so no AHEI component can move an outcome in the opposite direction from the others. How many cone constraints are active in the fitted solutions, and for which outcomes? This determines whether the cone reflects the data or imposes a structure on it. I suggest reporting the component signs in the unconstrained ablation (Table 2) to show whether some components take opposite signs and, if so, for which outcomes.
  4. Table 3 identifies the total score with κ = ∞, which equalizes weights on the cohort-standardized components; this is not equivalent to the AHEI total (equal weights on raw 0–10 scores). Please clarify in the text that κ = ∞ corresponds to equal weights on the standardized components, not to the AHEI total, and please also report the total-score results (Tables 2–3 and the total-score Wald test) with the actual AHEI total.
2 comments
AuthorsOpenReview ↗

Response to Reviewer mz2E: Part 1

Thank you for a very careful review and for catching a real gap in our proof. Your summary of what the paper does and does not show is accurate and it helped us reframe the paper. Below we answer each point and say where the revised paper changes.

Presentation and contribution

Thank you for pointing out where the presentation hid the contribution. We reorganized the revision around explicit claims and the evidence for each one.

  • A new claims-and-evidence table (Table 4, at the start of the appendix, pointed to at the top of Section 5) lists every claim with its evidence. It separates what is supported on the real cohort, what is shown on synthetic data, and what is not established.
  • Appendix A has a numerical example with two diet components and one pair. It shows the exact decomposition and what the cone constraints do.
  • Appendix B collects the notation and definitions in one place, including skill, anchoring, diet timing and cross-fitting.
  • Figure 1 now uses plain labels, with the equations in the caption.
  • Secondary analyses moved to the appendices. The main text keeps the findings and points to the tables.

Digital twin framing

You are right that our evidence does not support that use, and we changed the paper to match the evidence.

  • The method is now called the Signed Choquet Trajectory model (SCT). Digital twins remain only as a long-term motivation.
  • The contribution is a signed Choquet diet estimator, inside a partially linear longitudinal model, whose diet objective is solved to its global optimum given the fitted networks and settings. It comes with a scan-free bridge from body measurements to a frozen 3D generator.
  • We do not claim causal effects of an intervention, findings for single diet components, or validated what-if predictions for individuals.

The synthetic experiments ask whether the estimator can recover a signal when the true structure is known. There, the diet term improves skill in all 25 runs, and the model recovers 85 to 111% of the overall planted effect in seven of eight outcomes, with an overestimate for insulin. These results test what the estimator can do under known conditions. They do not show that the model is ready to be used as a digital twin, and they do not show causal validity for individuals in the real cohort.

Question 1: the orthogonality proof.

Thank you for finding this error. The old appendix argued that the loss is flat in the nuisance functions, which is not the right property. Appendix A now proves orthogonality of the estimating score, that is, the derivative of the loss with respect to the diet coefficients. At the true parameters:

  • The derivative with respect to the outcome nuisance is zero, because the residualized diet features have conditional mean zero.
  • The derivative with respect to the exposure nuisance has two terms. One is zero because the outcome error has conditional mean zero. The other is zero because the residualized diet features have conditional mean zero.

This shows Neyman orthogonality of the score without the penalty. In Section 3.3 we now keep this property apart from the distribution of the constrained and penalized estimator. A solution in the interior of the cone avoids the boundary problem, but the bias from regularization and any active constraints still need their own analysis. Orthogonality alone does not give standard confidence intervals for the full estimator.

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Response to Reviewer mz2E: Part 2

Question 2: which intervals are valid?

Appendix C and the Table 3 caption now separate three uses of the uncertainty estimates.

  • Standard inference from the orthogonal score covers the unconstrained coefficient on the equal-weight score and the Wald tests in the unconstrained additive model. It holds under the corresponding model and regularity assumptions.
  • Approximate intervals are the participant-bootstrap intervals for our model's overall association at the selected anchor, with the nuisance networks and settings held fixed. On synthetic data, they contain the true effect for seven of eight outcomes at the relevant anchor settings. This supports using them as approximate intervals but does not show that they reach nominal coverage.
  • Exploratory summaries are the anchored component contributions, the pair weights and their intervals. They support no claim of significance for any component.

To your direct question: the component and pair intervals at the selected anchor are not meant to support any claim, and we removed the component ranking from the main text. For questions about components, Table 14 gives a separate unconstrained additive analysis with participant-clustered intervals and a Holm correction across the 11 components within each reported outcome. No component remains significant. The smallest adjusted p-value is 0.07, for trans fat and weight.

All reported inference is evaluated at the selected diet timing and onset and does not account for the whole model-selection procedure.

On holding the networks fixed, we ran repeated cross-fitting. We drew five new fold assignments, retrained the networks for each, and combined the six estimates by the median.

  • The weight estimate is -1.22 kg (95% interval -1.73 to -0.71).
  • Compared with the fixed-network analysis, the standard error changes by a factor of 0.97 to 1.16 for weight, waist, blood pressure and insulin.
  • For insulin resistance (HOMA-IR) it grows by a factor of 1.49, though its interval still excludes zero.

So the main associations are stable, and refitting the networks matters more for insulin resistance. These repeated-cross-fitting intervals use a normal approximation, so they are a different kind of interval from the percentile bootstrap intervals in Table 3.

Question 3: how often is the cone active, and does it impose signs on the data?

Yes, the cone makes an assumption, and we now state it openly: improving any diet component moves the outcome in the same direction as a better overall diet, or leaves it unchanged. The AHEI scoring, where higher means healthier for every component, motivates this assumption but does not prove it for every outcome. The overall direction is not fixed in advance; it is estimated by comparing the two cones.

Table 6 now reports how many of the 11 constraints bind, averaged over runs at the selected settings:

  • about one for weight and waist;
  • one to two for blood pressure and insulin;
  • about three for insulin resistance and the outcomes without a clear association;
  • about four to six without anchoring.

Some estimates from the unconstrained additive fit do have the opposite sign. For weight, examples are sugar-sweetened drinks (+0.01 kg) and polyunsaturated fat (+0.20 kg). None of these remains significant after the Holm correction.

So in the additive analysis we tested, the data give no statistically clear contradiction of the assumption. That is weaker than proof that the assumption is correct, and we say so. The constrained fit also has a lower cross-validated loss than the unconstrained additive fit for every outcome except glucose. We therefore present the cone as a real modelling assumption that also helps as regularization.

Question 4: infinite anchor is not the AHEI total

You are right. The infinite-anchor fit puts equal weights on the standardized components, while the AHEI-2010 total puts equal weights on the raw 0–10 scores. We now keep the two apart throughout and have added the AHEI total as its own fit and its own restriction test.

  • Table 2: the AHEI-total fit has the same reported skill as the equal-weight fit. Its weight association is -1.00 kg (SD 0.31 kg across runs) and is negative in all 25 runs.
  • Table 13: on the whole cohort, the AHEI total's association with weight is -1.30 kg (95% interval -1.83 to -0.77). The intervals for waist, insulin and insulin resistance also exclude zero.
  • Table 7: the restriction test for weight gives p = 0.08 for the AHEI-total direction. Glucose is the only outcome where the restriction is rejected without adjustment. We do not read these p-values as showing that one score fits better than the other.

Anchoring toward the AHEI-total direction gives the same reported cross-validated loss and similar overall associations. The distinction is now explicit, and the main conclusions do not change.

Thank you again. We hope the revision shows that the paper's claims are now both well bounded and clearly presented.

Comments on the paper

1 comment

We thank all three reviewers for careful and constructive reviews. We have revised the paper to make the methodological contribution clearer, to widen the comparisons, and to bring the claims in line with the evidence. Below is a short summary. Each reviewer also gets a detailed reply.

New experiments

  • We added three kinds of baseline models:

    • a linear mixed model with a random intercept and a random slope for each person;
    • an explainable boosting machine with pairwise interactions;
    • a neural network trained end to end with longitudinal diet features, plus the same network without any diet input.
  • Every difference in accuracy now has a 95% interval from a paired bootstrap over participants, together with a second comparison based on cross-fitted forecasts.

    • Our model is ahead of ridge regression, the mixed model, gradient boosting, the explainable boosting machine, and the end-to-end network with diet.
    • Its accuracy cannot be told apart from that of the network without diet. So the gain in accuracy comes mainly from modelling the trajectory with a neural network.
  • We estimated the dietary associations again in four ways:

    • using only diet reported before each outcome visit;
    • with the AHEI-2010 total score;
    • with each of the two studies fitted on its own;
    • with each diet imputation fitted on its own.

    The associations with lower weight, smaller waist and lower insulin hold across the analyses where they apply. Under start timing, insulin resistance (HOMA-IR) is inconclusive at the 95% level.

  • We added checks on stability and sensitivity:

    • we redrew the cross-fitting folds and retrained all networks. The uncertainty changed only modestly for most outcomes, and it grew more for insulin resistance;
    • we counted how many cone constraints are active;
    • we estimated each diet component without constraints, with participant-clustered intervals and a Holm correction;
    • we refitted on random subsets of participants;
    • we added approximate E-values, which describe how sensitive the result is to unmeasured confounding.
  • We added two imputation checks:

    • baseline measurements: nearest-neighbour imputation with ten neighbours, fitted on training participants, gives results similar to mean imputation;
    • diet scores: ten imputed diet datasets instead of five give almost the same result. For weight, the combined estimate is -1.29 kg (95% interval -2.10 to -0.47) with ten, against -1.25 kg (-2.03 to -0.48) with five.

Changes to the text

  • The method is renamed the Signed Choquet Trajectory model, so the short name SCT stays the same.
  • We now lead with what is new in the estimator: an exact description of the valid diet weights as two cones, a global optimum of the diet objective given the fitted networks and settings, and a scan-free bridge to a frozen 3D generator.
  • Digital twins remain only as a long-term motivation. We separate adjusted associations from causal effects of an intervention, and we do not claim validated what-if predictions for individuals.
  • We corrected the proof of score orthogonality, and we now separate standard, approximate and exploratory inference.
  • We separated the equal-weight score on standardized components from the AHEI-2010 total, and we clarified which diet inputs the end-to-end network receives.
  • We removed the ranking of components from the main text, and we separate the exact decomposition, which is mathematical, from what the cohort can show about single components.
  • To make the paper easier to read, we added:
    • a claims-and-evidence table (Table 4, at the start of the appendix);
    • a worked numerical example;
    • a notation table;
    • a simpler Figure 1.
  • We moved secondary analyses to the appendices, so the main text stays within nine pages.

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

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