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Under review as a conference paper at ICLR 2027

TEMPOBRIDGE: SOURCE-CONDITIONED FLOW MATCHINGWITHOPTIMALTRANSPORTCOUPLINGS FORSINGLE-CELLPOPULATIONTRANSITIONS

Abstract

Destructivesingle-cellmeasurementsprovideunpairedpopulationsnapshotsrather thanobservationsofthesamecellsacrossconditions.Localcellstatesandtran sitionrequestsmayalsobeinsufficient todistinguishresponsesacrosssource populations.WeintroduceTempoBridge,acommonsource-conditionedtransport formulationfortemporal,genetic,andchemicalpopulationtransitions. Source cellsinitializelatenttransportandprovideafixedempiricalpopulationsummary. Thevelocityfieldreceivesthissummaryalongsidetheevolvingcellstate,flow time, andastructuredtransitiondescriptor. Minibatchoptimal transport (OT) suppliescouplingsonlyforconditionalflow-matchingtrainingpaths; inference requiresneithertargetexpressionnorOTcomputation.Onheld-outdonors,Tem poBridgeachievesanEnergydistanceof0.129versus0.144forscGen.Genetic mean-expressionL2erroris2.261versus3.156forscGPT-scratchunderSeen2/2. Onheld-outcompounds,condition-averageddrug-effectcorrelationis0.598versus 0.561fortheCellFlowadapter.Temporalablationsshowhighermeandistribu tionalerrorafterremovingsourcecontext,replacingoptimaltransportwithrandom pairing,orreplacingflowmatchingwithstaticresidualregression.Together,these resultsdemonstratethepredictiveutilityofacommonsource-conditionedtransport formulationacrossheld-outdonors,genecombinations,andcompounds.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Single-cell genomics, Population transition prediction, Conditional flow matching, Optimal transport, Source-population conditioning, Perturbation prediction

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_LdwkOpenReview ↗
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Paper summary

The paper proposes a latent OT-CFM model whose velocity field is also conditioned on a mean-pooled embedding of the source population and on a transition descriptor. The method is evaluated on held-out donors in iPSC differentiation (Cuomo), unseen Norman Perturb-seq combinations, and unseen sci-Plex3 compounds.

Critical strengths

The evaluation is overall well done and presents results in a honest way. Experiments state clearly what the model can see of the targets, and they separates swapped-context controls from matched retraining. A single formulation covers temporal, genetic and chemical tasks. The synthetic ambiguity experiment is clean.

Critical weaknesses

I have found the paper to be overall a fairly hard read despite the simplicity and limited methodological novelty (in a ML sense) of the paper. The introduction is in that sense quite vague and should do a better job of highlighting the main differentiator, methodolofically, compared to previous work. More precisely:

  1. Conditioning a flow on an embedding of the initial population is the central idea of Meta Flow Matching (Atanackovic et al., 2024), which is neither cited nor compared against. Schrodinger-bridge and multi-marginal trajectory methods (e.g. SF2M) are also missing. A very similar idea (although not flow based) is proposed in "Supervised Training of Conditional Monge Maps" by Bunne et al. 2022.
  2. The theory in App. B.5 reduces to the standard fact that conditioning on more variables lowers the Bayes risk. It does not show that real data contain this ambiguity, or that mean pooling keeps the relevant information.
  3. On real data, the benefit of source context is small or mixed. In the matched retraining (Table S13), Energy is 0.135 vs 0.139, and r and DE@100 favor the model without context. In the genetic task the source panel is fixed, so the context is constant and the model reduces to conditional OT-CFM with auxiliary losses.
  4. The reported standard deviations vary only the test seed. The auxiliary losses directly optimize the evaluation metrics. The pEnergy of the CellFlow adapter (9.22) suggests a broken baseline.
Questions for authors
  • How does the method differ from Meta Flow Matching, and how do the two compare empirically?
  • How much do results vary across training seeds?
  • How does the model perform without the auxiliary losses?
  • Did you try richer set encoders than a mean?
  • What batch sizes did you use for Sinkhorn? Where do the different epsilon/num iteration settings come from across experiments and why did you change them?

minor:

  • "Because sequencing destroys measured cells, training provides unpaired source and target populations rather than trajectories of the same cells (Schiebinger et al., 2019)" -> training provides, in what sense is "training" the subject of the verb "provides"?
3 comments

Thank you for the careful review.

W1/Q1. Meta Flow Matching (MFM). Atanackovic et al. condition a flow on the starting population. Both methods can predict intermediate states. MFM aggregates across neighbours before pooling. TempoBridge averages individual cell embeddings and uses that summary throughout the flow.

Our donor swaps test whether a fitted model uses source context (S14). Matched retraining tests whether providing that context improves prediction (S13).

The Cuomo pipeline is our adaptation of the authors' released TrellisMFM graph encoder and velocity network. On a synthetic batch, our adapter reproduced the embeddings and integration obtained by calling their networks directly. We matched source cells, expression encoder initialization, auxiliary losses and checkpoint selection by validation MMD. We trained on Day 0 to Day 3 and tested on Days 1 and 2 in 15 held-out donors (2,009 genes). T2 and MFM used random pairing within donors.

ModelEnergy (SD) ↓MMD ↓Effect r ↑DE@100 ↑
TempoBridge, OT (T1)0.1383 (0.0101)0.38380.63420.5235
TempoBridge, random (T2)0.1366 (0.0109)0.37990.62230.5181
MFM adaptation, random0.1449 (0.0058)0.40860.62630.5140

Both TempoBridge variants had lower mean Energy (our primary metric) than MFM. Under matched random pairing, T2 had lower Energy and MFM had higher effect correlation. Within TempoBridge, S4 favoured OT at fixed checkpoints (0.1291 vs 0.1446). In the comparison above, random pairing had lower mean Energy (0.1366 vs 0.1383).

W2/Q4. Theory and pooling. Appendix B.5 applies the squared-error Bayes risk identity. With the coupling and paths fixed, source information lowers the minimum error if mean velocity still depends on the source given cell state, time and condition. Table 4 gives one example. How often this occurs in real data, and whether the mean retains the signal, remain open. The MFM and SCALE-style comparisons use richer encoders but also change the predictor, so neither isolates pooling.

W3. Source context. In S14, we changed only the donor summary. For 12 of 15 donors, Energy with their own summary was lower than the average obtained with the other donors' summaries.

In S13, with three training seeds each, mean Energy (SD) was 0.1350 (0.0051) with source context and 0.1393 (0.0133) without it. Effect correlation and DE@100 favoured training without context. A classifier fitted on training donors showed that context reduced stage-proportion error by 4.7739 percentage points on Day 1 and 1.2593 on Day 2, though Day 1 error remained high at 89.5173 points. The genetic task uses the same 128 controls throughout, so its source panel is fixed.

W4/Q3. Genetic auxiliary losses. In Seen 2/2 both genes appeared in training, but their combination was new. Some losses directly supervise quantities we evaluate, including mean expression. We removed all seven population losses together, keeping flow matching and both reconstruction losses.

SupervisionMean L2, OT ↓Mean L2, random ↓Energy, OT ↓Energy, random ↓
Full (mean-loss weight 100)2.27512.25470.48180.4786
Seven losses off3.71813.78950.84190.8920

Removing the losses increased both mean-expression error (Mean L2) and distributional distance (Energy), and also raised both errors on the other two splits with OT. In Seen 2/2, OT gave lower errors than random pairing with the losses off. Under full supervision the errors were similar.

CellFlow baseline. Compressing measured target cells to 50 principal components and reconstructing them gave a projected Energy of 9.4106 before prediction. We retrained our adapter on all 2,000 genes, keeping the test cells and evaluation projection fixed. Projected Energy fell from 9.2228 to 0.2874 (TempoBridge, 0.2123), while effect r fell from 0.5608 to 0.0805. The original adapter overstated our distributional advantage.

Q5. Sinkhorn settings. Each plan pairs cells within one record. For biological tasks we divided squared latent distances by their within-record median.

TaskSource × target cellsεIterationsRecords/update
Temporal retraining64 × 640.0300200256
Genetic128 × 1280.0500308
Drug128 × 1280.050010064
Synthetic (Table 4)64 × 640.05005016

We kept each task's original settings. No common tuning rule was documented. The earlier four-GPU temporal setup specified 1,024 records per update.

Manuscript changes. We will refocus the Introduction on when source context helps and credit MFM, SF²M and conditional Monge maps. We will add these comparisons and settings, correct the CellFlow row, and revise the flagged sentence to read "Because single-cell RNA sequencing destroys each assayed cell, we observe unpaired source and target populations."

Reviewer_LdwkOpenReview ↗

Thanks for your rebuttal

Thanks for your experiments.

  • I find it a bit discouraging to see on these experiments (W1) that your OT variant has higher energy & MMD than random (independent) coupling. I feel this "kills" a part of your story when OT is no longer useful, or even detrimental.
  • I am a bit skeptical of your Sinkhorn settings. Why set #max iterations (perhaps your solver did not converge?) rather a convergence threshold (as usual). How did you set your batch sizes? It feels that n of the order of 64~128 is way too small to be robust. In particular you wrote "No common tuning rule was documented", what does this mean? documented by whom?

Since the OT part is a bit flawed and incomplete as it stands, yet takes a prominent role in your framing, I suggest that you revisit these aspects and dive more into whether changing key quantities (batch sizes, preferably increased or even max-ed to total data sample size) or epsilon could reshape your results. You could for instance report KL of your coupling to independent coupling as a natural metric to reflect the "peakyness" of your couplings, rather than just put the table you provided that has been tuned... in "some" way? (I could not understand what you meant and "No common tuning rule was documented" seems very LLM-ish)

Overall I am grateful to the authors for their improvements and efforts, but I think the paper still needs a solid round to (a) have results that are more consistent with the story line (i.e. where minibatch OT consistently wins, and we understand at what regimes) and (b) do the required ablations and keep on turning the screw where needed (e.g. CellFlow).

Thank you for asking whether a larger pool of cells would help OT. In the temporal task, increasing the pool from 64 to 128 cells per side gave couplings closer to those computed from all available cells in each record. It did not improve prediction.

Six training records had at least 128 cells on both sides. We used the same six records at both pool sizes, fixed ε at 0.03, and sampled 64 training pairs per record. To compare the couplings, we first computed a reference using all available cells in each record. We took the part of that reference corresponding to the sampled cells and renormalized it. The mean total variation distance from this reference fell from 0.1745 at 64 cells per side to 0.0967 at 128. Eleven of the twelve training runs finished. For the two seeds with all four settings complete, increasing the pool raised OT’s mean test Energy from 0.1315 to 0.1371 and its mean test MMD from 0.3521 to 0.3664. Lower values are better for both metrics.

Sinkhorn settings. Each temporal training update sampled 256 records. We solved a separate coupling for each record using 64 source cells, 64 target cells, ε = 0.03, and 200 iterations. Our earlier phrase “no common tuning rule was documented” referred to our own experiment records, which list the settings used for each task. We will report the number of cells per coupling, ε, and the number of Sinkhorn iterations for each task in the main text.

To check whether 200 iterations were enough, we replayed the first training batch for each of three seeds (768 couplings) and drew 300 more samples at three frozen checkpoints. At 200 iterations, 1,044 of the 1,068 couplings met a marginal L1 tolerance of 10⁻⁴ on both sides. At 500 iterations, all 1,068 met it. Even after extending the runs to 2,000 iterations, the total variation distance from the 200-iteration solution was below 0.000233 for every coupling we checked.

We also tested whether more iterations improved prediction. We trained two models with seed 42 using the same initial weights and cell samples, then evaluated them on the same 15 held-out donors. Increasing from 200 to 500 iterations raised test Energy from 0.13141 to 0.13219 and test MMD from 0.34759 to 0.35763. The extra iterations improved numerical accuracy in the coupling check, but neither test metric improved in this run.

Effect of ε. With 64 cells per side, mean KL divergence from independent coupling fell from 2.06 at ε = 0.015 to 1.14 at ε = 0.03 and 0.46 at ε = 0.06. We tested all three values in matched training runs with seed 42 and 200 Sinkhorn iterations. At the original ε = 0.03, test Energy was 0.13141 and test MMD was 0.34759. Halving ε to 0.015 raised Energy to 0.13550 and MMD to 0.35633. Doubling ε to 0.06 raised Energy to 0.13234 and MMD to 0.35759. These results support keeping ε = 0.03 for this task. Halving or doubling it changed the couplings, with modest increases in test error for this seed: 0.7%–3.1% for Energy and 2.5%–2.9% for MMD.

Contribution. MFM models how cell velocity can depend on the starting population, and SCALE uses a population summary to predict the treated endpoint. Our contribution is to quantify the cost of omitting source information in velocity prediction and to test separately whether a model uses that information and whether it improves predictions. With pairings and paths fixed, two source populations can have different mean velocities at the same cell state, flow time, and transition. If this occurs with positive probability, omitting the source raises the minimum achievable mean squared velocity error (Section 3.2 and Appendix B.5).

Both models in the pairing comparison received the same source summary. We tested the role of the summary in two separate experiments. Swapping donor summaries changed predictions while the model weights and starting cells were held fixed. In matched retraining, adding the summary reduced Day 1 cell-state composition error in all three seeds, by 4.77 percentage on average. Effect correlation was higher without the summary.

CellFlow. We checked whether the 50-component PCA representation in our CellFlow adapter could account for the high projected Energy. Compressing and reconstructing the measured target cells alone gave a projected Energy of 9.4106, before any prediction. We then retrained the adapter on all 2,000 genes, using the same test cells and evaluation projection. Its projected Energy fell from 9.2228 to 0.2874, while its effect correlation fell from 0.5608 to 0.0805.

Reviewer_YRAEOpenReview ↗
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Paper summary

TempoBridge conditions latent OT flow matching on a fixed, mean-pooled summary of the source population alongside the evolving cell state and transition descriptor. Separate models address temporal differentiation, genetic perturbations, and drug responses. The paper motivates source conditioning through an ambiguity construction and evaluates complete models, context swaps, and selected component ablations.

Critical strengths
  1. The information argument is clear and testable. The shared-state synthetic example and donor-context swaps demonstrate why an individual cell and a transition label may not contain all relevant source information. These are more informative than a performance table alone.
  2. The complete models show useful predictive performance. Temporal Energy distance improves over scGen, and the genetic model has strong mean-response results, particularly for Seen 2/2 combinations. Evaluation spans several meaningful types of held-out biological conditions.
Critical weaknesses
  1. The methodological advance over existing population-conditioned transport is modest. Mean-pooled source context, conditional flow matching, and minibatch OT are established ingredients; the paper itself cites set-aware conditioning in SCALE. The ambiguity argument motivates additional conditioning but does not establish a distinctive new transport principle. A direct comparison with the closest population-aware alternative is absent.
  2. The main gains are not convincingly attributable to the central idea. Matched temporal retraining changes Energy from 0.139 to 0.135 but worsens effect correlation and DE@100; drug source-context gains are small and metric dependent. The genetic task uses a fixed source panel and a substantial auxiliary-loss recipe, including a mean loss weighted by 100 (Appendix C.4), so its strongest results do not establish the value of source conditioning or OT flow. This leaves a gap between the paper's central explanation and its headline evidence.
Questions for authors
  1. Clarification and comparison: What capability is added beyond set-aware source conditioning such as SCALE, and does that distinction produce a measurable advantage under matched inputs and supervision?
  2. Assessment-critical comparison: Do the genetic and drug advantages persist when simpler conditional predictors receive the same representation, source context, auxiliary losses, and selection criterion? Which improvement remains attributable to OT flow itself?
1 comment

Thank you for the questions.

W1/Q1. What does TempoBridge add beyond SCALE?

SCALE fuses a population summary into each cell representation and predicts the treated endpoint. TempoBridge uses a mean source summary as a separate input to a latent velocity field trained with OT pairs. The input placement and training target differ; the conditioning principle is the same.

Our contribution is a boundary that population conditioning has not been tested against. When does information from the rest of a sample change a prediction that already uses the cell state and transition? Section 3.2 and Appendix B.5 state this formally. We test context use and predictive benefit separately. Either answer informs design. The results are mixed: benefits are real, local, and setting-dependent.

To answer Q1, we compared TempoBridge with our SCALE-style implementation on 19 unseen drugs and 248 conditions, matching cells, inputs, encoder, supervision, budget, and validation rule. Projected Energy was the prespecified primary metric. Three-run means, with equal drug weights: projected Energy was 0.1829 versus 0.2300, lower for TempoBridge in all three runs, while effect correlation was 0.3955 versus 0.4340, favouring the comparator. The advantage is therefore on the primary metric, not on effect correlation. This is our implementation, not official SCALE code.

W2. What biological information does source context add?

With weights and starting cells fixed, 12 of 15 donors had lower Energy with their own summary than the mean Energy over other donors' summaries (Table S14). Matched retraining was mixed: context lowered Energy from 0.1390 to 0.1350, while effect correlation and DE@100 favoured no context (Table S13). Context use therefore does not imply predictive benefit.

A classifier fitted only on training donors estimated cell-state proportions. Labels follow public pseudotime rules, not measured lineage. On Day 1 it assigned 99.2677% of measured cells to mesendoderm, versus 5.0088% of predictions without context and 9.7504% with it. Mean total-variation composition error fell by 4.7739 points, improving in all three runs; the Day 2 reduction was 1.2593 points, improving in two.

Context therefore reduces underprediction of the dominant Day 1 state. The remaining error is large. Both models miss the Day 1 mesendoderm peak in every donor and seed. This is a partial composition gain rather than recovery of the differentiation process. Sparse-input results reverse on Day 1, and extra cells with biased checkpoint selection limit that comparison.

For drugs with a fixed encoder, context raised effect correlation from 0.4220 to 0.4250 but worsened projected Energy from 0.1930 to 0.1970 (Table S10). Genetics uses the same 128 control cells throughout, so it tests new perturbations from a fixed source.

Q2. Do the gains hold with matched inputs and supervision?

We compared OT flow, random-pair flow, and a one-step residual MLP. All received the same cells, context, perturbation inputs, population losses, loss weights, and validation rule. Genetic encoders and decoders started identically, then trained separately. Their final representations can differ. Drug models shared a frozen source encoder and decoder initialization.

Three-run means. Drug rows weight conditions equally; the SCALE comparison weights drugs equally. Seen counts genes in a held-out pair that appeared in training perturbations.

Setting/metricOT flowRandom flowMLP
Seen 2/2, Mean L22.27512.25472.2124
Seen 2/2, Energy0.48180.47860.4680
Seen 1/2, Energy1.06881.07141.0975
Seen 0/2, Energy0.97440.97420.9842
Unseen drugs, projected Energy0.19240.19220.2280
Unseen drugs, effect correlation0.40630.40730.4243

Both flows beat MLP on drug Energy at all three seeds. OT beat MLP on Seen 1/2 at all three seeds. MLP was best on both Seen 2/2 metrics and drug effect correlation. Both flows had lower mean Energy than MLP on Seen 0/2. These gains depend on the metric and cannot be attributed to context, which all predictors receive.

W2/Q2. How much comes from OT and the auxiliary losses?

On Seen 2/2, disabling seven population losses raised OT Mean L2 from 2.2751 to 3.7181 and Energy from 0.4818 to 0.8419. Without them, random pairing gave 3.7895 and 0.8920. OT was better at all three seeds. Under full supervision, random pairing had slightly lower mean errors. The losses raised effect correlation from 0.7969 to 0.9154 (OT) and 0.7902 to 0.9171 (random). Genetic results therefore depend strongly on auxiliary supervision, and this joint ablation does not isolate the mean-loss term or test its weight of 100.

Planned revision. We will present the boundary and these results as the contribution rather than a new transport method. We will place matched comparisons beside the main results and explain what each metric measures.

Reviewer_y7KxOpenReview ↗
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Paper summary

In this work, the authors propose TempoBridge which is a source conditioned flow matching method that uses unpaired observations to predict single cell population transitions. They do so by conditioning the velocity field on a mean-pooled representation of the initial source population and then evolve the cell state and the transition itself. They use minibatch OT to build the training pairs for conditional flow matching and, then at inference time, it only needs the source cell and requested condition. Subsequently, they also call the pointwise conflict a source dependent transition ambiguity and evaluate on different prediction settings such as genetic perturbations and drug responses and temporal differentiation. Finally, the paper also have may ablations and shows performance across different synthetic tasks to motivate why they do source conditioning.

Critical strengths

The paper provides a very good empirical evaluation on different distributions and biological metrics and settings too. They also gave multiple different baselines with useful ablations and a lot of specific details for reproducibility. In terms of results, they also show that, in a controlled setting, having source context improves the branch accuracy from 50% to 90%, which motivates the problem of studying these type of conditioned transport in cell states.

Critical weaknesses

I found the writing in the paper very confusing and that the results would have benefited from more meaningful discussion/implications and insights about such improvements. There are also several weaknesses to this paper:

  1. It is not clear to me exactly what is unique and novel/new here in terms of the modeling that is being done compared to existing works. As the authors have highlighted in the related work, there has already been some work on OT-CFM and mean-pooled source representations and conditional velocity networks and fields. It seems to me that this is just some sort of source conditioned transport model on a population level.
  2. Some parts of the experiments are also very unclear about whether source conditioning is actually useful, which is the main contribution of the paper. Like in the match temporal training setting, the source context only slightly improves from 0.139 to 0.135, but even the no context does better on the correlation and on DE@100.
Questions for authors
  • What is the benefit of having or doing source conditioning in these biological datasets since we see that the improvements are all quite metric-dependent and very marginal in the ablations as well?
  • How does the method do vs non-OT conditional methods if you give it the same supervision and encoder and decoder? This is not asking for another baseline, just curious whether having any continuous transport will lead to improvements generally.
3 comments

Thank you. We address novelty, context benefits, and direct predictors.

W1. What is new beyond the existing components?

OT-CFM, mean-pooled source summaries, and conditional velocity fields are established components. TempoBridge uses them in a latent model. It averages encoded source cells once and supplies this fixed summary separately to the velocity field at each step.

Our contribution is the analysis of when source information is needed and tests that separate context use from predictive benefit. For fixed couplings and paths, sources with the same transition label can require different mean velocities at the same state and flow time. A field without source information cannot match both. Section 3.2 and Appendix B.5 bound the extra squared risk when this conflict has positive probability. A source summary can resolve the conflict if it retains the relevant differences.

In Table 4, branch accuracy is 98.04% with correct context, 50.00% without, and 1.96% with swapped contexts; correct and swapped cases use the same model. With weights and test cells fixed, 12 of 15 held-out donors have lower Energy with their own context than the mean Energy over other donors' contexts (Table S14). These tests show that the model uses context. Matched retraining tests whether context improves prediction.

Against our SCALE-style implementation on unseen drugs, projected Energy is 0.1829 versus 0.2300 and effect correlation 0.3955 versus 0.4340. TempoBridge better matches the distribution; the comparator better captures mean-response patterns. The comparator is our implementation, not official SCALE code.

W2/Q1. What does source context help predict?

Source context reduces a specific composition bias, but gains depend on the setting and metric. In temporal matched retraining, Energy falls from 0.1390 to 0.1350, but effect correlation and DE@100 worsen (Table S13).

Biological evaluations used the same six checkpoints. A classifier fitted on training donors estimates state proportions in measured and predicted cells; labels follow public pseudotime rules, not lineage. On Day 1 it assigns 99.2677% of measured cells to mesendoderm, versus 5.0088% of predictions without context and 9.7504% with it. Total-variation composition error falls from 94.2912 to 89.5173 points, improving at all three seeds. The reduction is 4.7739 points (paired donor-bootstrap 95% interval 2.9899 to 6.7556, conditional on the fixed models).

Context thus reduces underprediction of the dominant Day 1 state, but the remaining error is large. Both models miss the mesendoderm program peak seen in 13 of 15 donors, and a median-progress baseline beats both on donor progress. We claim neither recovery of lineage nor of donor differentiation speed.

Sparse-input composition results are mixed: context worsens Day 1 and improves Day 2. Extra cells and biased checkpoint selection limit that exploratory comparison. In genetics all conditions share 128 control cells, so context is constant within a model. Drug ablations show metric tradeoffs (Table S10).

Q2. Flow, OT pairing, and direct prediction

We compared OT flow, random-pair flow, and a one-step residual MLP. All receive the same cells, context, and perturbation inputs, and the same population losses, weights, and validation rule. Genetic encoders and decoders start identically, then train separately; drug models share a frozen source encoder and decoder initialization.

On the temporal task, TempoBridge beat a time-conditioned MLP on both intermediate days (Energy 0.1306 versus 0.1543 on Day 1, 0.1277 versus 0.1471 on Day 2). That MLP uses a PCA representation, so this compares full methods, not the transport component alone.

Three-seed means; conditions weighted equally here, drugs equally in the SCALE comparison. Seen = genes per held-out pair perturbed in training.

Setting/metricOT flowRandom flowMLP
Unseen drugs, projected Energy0.19240.19220.2280
Unseen drugs, effect correlation0.40630.40730.4243
Genetic Seen 1/2, Energy1.06881.07141.0975
Genetic Seen 2/2, Energy0.48180.47860.4680
Genetic Seen 2/2, Mean L22.27512.25472.2124

Both flows beat the MLP on drug Energy at all three seeds; the MLP is best on both Seen 2/2 metrics and on drug effect correlation. All models receive context, so this does not isolate its benefit.

OT is not the main driver under full supervision. With the seven population losses removed, OT lowers Seen 2/2 Energy from 0.8920 to 0.8419; with all losses, random pairing gives 0.4786 versus 0.4818. Solver tests show small, setting-dependent gains and do not establish that flow generally beats direct prediction.

In the revision we will state these boundaries and place matched comparisons beside the main results. We will restructure the introduction around problem, limit, and approach with an explicit list of claims.

Thank you for the response and experiments, especially in clarifying the novelty and the better comparisons. The response has addressed some of my previous questions, but I am still concerned about the motivation and contributions. I am still unsure whether this means that the ambiguity is from flow matching vs population transition prediction; also it is still not clear to me whether there are any benefits of conditioning on this source information. Regardless, I will increase my score.

Thank you for raising your score and for explaining which questions remain.

MFM models how cell velocity can depend on the starting population, and SCALE uses a population summary to predict the treated endpoint. Our contribution is to quantify the cost of omitting source information in velocity prediction and to test separately whether a model uses that information and whether it improves predictions. In our flow-matching analysis, the pairings and paths are fixed. Two source populations can still have different mean velocities at the same cell state, flow time, and transition. The ambiguity arises when the predictor has only those inputs and must give the same answer for both populations. If this happens with positive probability, omitting the source raises the minimum achievable mean squared velocity error (Section 3.2 and Appendix B.5).

When we held the model weights and starting cells fixed, swapping donor summaries changed the predictions. To test whether the summary helped, we retrained temporal models with and without it under the same conditions. On Day 1, the same classifier labeled 99.27% of measured cells as mesendoderm. Among predicted cells, that proportion rose from 5.01% without the summary to 9.75% with it, reducing the underestimation of the dominant state. Effect correlation was higher without the summary. Adding the summary reduced the overall Day 1 composition error across all four cell states in all three training runs. The average reduction was 4.77 percentage points.

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