Treating the Dish as a Survival Study: Linking Motor-Neuron Death in Culture to ALS Patient Survival

Stem cells can be grown from a patient's blood and turned into motor neurons. The resulting neurons carry the patient's full genome, and in culture they die at rates that differ from patient to patient. Clinicians, separately, model how long patients survive using hazard models, which describe the instantaneous risk of an event such as death, given that it has not yet happened. We propose to join the two. The death of each neuron in a time-lapse microscopy experiment is analysed as a time-to-event outcome in its own right. From that analysis we estimate a latent "cellular vulnerability" for each donor, after removing the variation that comes from the lab batch in which the cells were produced. The same latent quantity then enters the patient's clinical hazard of death or respiratory failure, and both levels are fitted in one likelihood. If the link is real, the dish gives a functional prognostic signal that clinical tables and brain MRI have so far failed to provide.

Why now: the Answer ALS resource reprogrammed blood from 1,047 participants into induced pluripotent stem cells (iPSCs, adult cells returned to an embryo-like state) and made spinal motor neurons from more than 850 lines. It tracked neuron death with longitudinal robotic microscopy and collected longitudinal clinical ratings (the ALSFRS-R functional scale). It showed that neurons from SOD1-mutant patients die faster. However, it related molecular pathways to clinical decline only through correlations with the ALSFRS-R slope. It never fitted a survival model connecting cell death to patient time-to-event outcomes, and it treated batch variability as a correction step rather than as part of the model. On the clinical side, Tang et al. found that adding 68 MRI cortical-thickness features to 114 clinical variables gave no significant gain in predicting ALS respiratory failure. So the open question is sharp: can cellular-scale function succeed where macro-scale imaging did not?

Core Claim

The core claim is that cell-death data from a microscope are themselves censored survival data. A neuron that is still alive when imaging stops, or that drifts out of the field of view, has an unobserved death time, just as a patient lost to follow-up does. Much of the noise in these data comes from the differentiation run, not the donor. Collapsing each line to a single "fraction dead by day X" throws away the censoring structure. It also confounds donor biology with the run, and it hands the clinical model a noisy covariate whose measurement error shrinks its apparent effect toward zero.

A crossed-frailty joint model addresses all three problems. A frailty is a multiplicative random effect shared by a group of observations that captures unobserved risk common to that group. Our model has a donor frailty and a run frailty that are separately identifiable. Only the donor frailty is allowed to enter the clinical hazard. The measurable prediction follows directly: the estimated association between cellular vulnerability and clinical survival should be larger and better calibrated than under naive two-stage pipelines. Crucially, the association should persist among sporadic patients with no known pathogenic variant, who are 88% of Answer ALS cases.

Model

Index donors by $d$, differentiation runs by $r$, and individual neurons by $n$, and let $s$ be time in culture. Each run processes many lines at once, so donor and run are crossed rather than nested. This crossing is what makes the two effects separable. The in vitro hazard of neuron death is

$$\lambda_{drn}(s) = \lambda_0(s)\, u_d\, v_r \exp(\gamma^\top z_{drn}),$$

where $\lambda_0(s)$ is an unspecified baseline hazard in culture. Here $u_d$ is the donor frailty (the cellular vulnerability we want), $v_r$ is the run frailty, and $z_{drn}$ holds technical covariates: motor-neuron marker status, local cell density, and the line's differentiation efficiency. The last matters because only about 34% of cells were motor neurons in Answer ALS. The patient's clinical hazard is

$$h_d(t) = h_0(t) \exp(\beta^\top x_d + \alpha \log u_d),$$

where $t$ is time since symptom onset, $x_d$ are baseline clinical covariates, and $\alpha$ is the quantity of scientific interest: how much the donor's cellular vulnerability scales their clinical risk. The run frailty $v_r$ is deliberately excluded from the clinical equation. That exclusion is a testable modelling assumption and the key ingredient the ablations isolate.

The joint likelihood integrates over $u_d$ and $v_r$. For the method, we reuse two ingredients. One is the Laplace-approximated penalized quasi-likelihood of Zhou et al., which added a cluster random effect to a neural Cox model for transplant facilities. The other is the frailty theory reviewed by Gorfine and Zucker, which documents the biased hazard ratios and inflated significance that result from ignoring clustering. Both treat a single level of clustering within one outcome. Here two crossed frailties span two outcomes on different timescales, one measured in days and one in years, which neither paper addresses.

We keep the clinical level linear. With a few hundred events, the linear-versus-deep comparison in DeepSurv argues against extra capacity: on linear simulated data, the linear Cox model matched DeepSurv, with C-index 0.779 versus 0.778. Neuron death in culture may not have proportional hazards across donors, for example an early wave of death in some lines and a late one in others. As a secondary variant, we therefore let the in vitro level be a two-component latent mixture in the style of Deep Cox Mixtures, which models survival as a mixture of latent Cox models to capture crossing curves. We check proportionality with Schoenfeld-type residuals before adopting it.

Research Program

The first phase is a simulation study calibrated to Answer ALS. We match the number of donors, the lines per run, the neurons per line, the censoring due to the imaging window, and the clinical censoring. Tang et al. report 45% censoring in CALSNIC, a separate ALS cohort, and we use that as a plausible range. Ground truth for $\alpha$ is known. We vary run-frailty variance from zero to large. This phase tells us whether $\alpha$ is recoverable at realistic sample sizes. It also tells us how much bias and attenuation each simpler pipeline suffers, and in particular whether the crossed design separates donor from run effects when each line was differentiated only once.

The second phase applies the model to Answer ALS. The primary endpoint is time from onset to death or to a respiratory milestone. Where tracheostomy or permanent ventilation is not recorded directly, the milestone is defined from the ALSFRS-R respiratory items. Death and censoring are taken from clinical follow-up. We define the endpoint before looking at the cell data. The third phase examines what $u_d$ reflects. We relate donor frailties to the RNA-seq, ATAC-seq and proteomic profiles of the same lines, asking which pathways track cellular vulnerability once run effects are removed. Frailty estimates are used as a low-dimensional target rather than feeding thousands of omic features into the clinical model.

The main feasibility risks are whether survival microscopy exists for enough lines, and how many clinical events have accrued. We do not know either from the file. If the event count is small, the deliverable shifts from a prognostic model to an estimate of $\alpha$ with honest uncertainty. That is still new.

Baselines

The naive reference point is a clinical-only Cox model using the variables Answer ALS records at baseline: age, onset site, diagnostic delay and ALSFRS-R slope. The closest reported number for clinical-only ALS survival prediction is a C-index of 0.70 with an MAE-margin of 14.2 months, against 17.4 for their baseline, from the SuperLearner in Tang et al. on CALSNIC. That is a different cohort, so it frames plausibility rather than serving as a target. We found no reported result on Lacuna for any survival model fitted on Answer ALS, so all Answer ALS baselines will be run by us. Kuffner et al. report that GuanRank beat standard Cox by 20% on PRO-ACT, but that relied on trial-scale data and was reported as a z-score. We will include a random survival forest on clinical variables as the strongest flexible clinical competitor.

The strongest competitor on the actual question is a two-stage pipeline. First, estimate each line's death rate with a per-line Cox or Kaplan–Meier fit, shrunk by empirical Bayes and adjusted for run as a fixed effect. Second, add that rate as a covariate to the clinical Cox model. A careful statistician would build exactly this. It shares our data, splits and endpoint. Its only difference is that measurement uncertainty is not propagated and the run adjustment is not modelled jointly. A second strong baseline uses SOD1/C9orf72/known-variant status in place of any cellular measurement. The ablations remove the run frailty (donor frailty only) and replace neuron-level censored data with a per-line "fraction dead at the last timepoint."

All models get the same cross-validation folds, which are stratified by run so that no run appears in both train and test. They also get the same covariates and the same hyperparameter search budget. Beating the field means three things on held-out donors: the joint model improves both C-index and integrated Brier score over clinical-only; it improves calibration over two-stage; and its estimate of $\alpha$ has a confidence interval excluding zero among sporadic patients.

Why not just…?

Why not just compute each line's death rate and put it in a Cox model? This is the real threat, and it may work nearly as well. If run variance turns out small, most lines are imaged over long windows, and shrinkage is applied, the two-stage estimate of $\alpha$ could match ours. Phase one quantifies in advance the conditions under which the joint model helps. The Answer ALS comparison then says which regime the data are in. If two-stage matches the joint model, we will report that and recommend it. The scientific finding about $\alpha$ would stand either way.

Why not just use clinical variables, since MRI added nothing? Tang et al. show that the clinical ceiling is hard to break. But cortical thickness is a structural endpoint of damage, whereas neuron death in culture is a functional readout of the donor's genome under stress. The comparison with the clinical-only baseline, reported with confidence intervals, settles this directly. A null result would be informative too.

Why not just use genotype, since the dish mostly recapitulates SOD1? The observed SOD1 effect in Answer ALS suggests cellular vulnerability could be a proxy for known mutations. We therefore fit the model within sporadic patients only and with genotype as a covariate. The contribution depends on $\alpha$ surviving both analyses.

Why not just feed omics or raw images into a deep survival network and let it absorb batch? Hundreds of donors cannot support thousands of features. Moreover, Zhou et al. show that DeepSurv falls to a C-index of 59.61 against 74.67 for a frailty network when cluster variance is high ($\theta = 3.5$, simulation). A DeepSurv model on omics, with run as an input, is included as a comparator to check this in our setting.

Proposed Experiments and Decisive Checks

Beyond the held-out C-index, integrated Brier score and calibration curves at 12, 24 and 36 months, four checks decide whether the claim holds. The central one is a sporadic-only, genotype-adjusted estimate of $\alpha$.

The second is a donor-permutation control. Cell data are reassigned to other donors within the same run, which should drive $\alpha$ to zero while leaving the in vitro fit intact.

The third tests the exclusion restriction. We refit the model allowing the run frailty into the clinical hazard; its estimated effect should be near zero, since a lab run cannot cause a patient's death.

The fourth concerns the healthy-control lines, which have no clinical event. Their donor frailties should sit below those of ALS patients. This checks that $u_d$ carries disease biology rather than technical noise.

Finally, consistent with the warning in Deep Cox Mixtures that ranking alone hides miscalibration, we report calibration error alongside discrimination for every model. A finding that the dish improves ranking but not calibrated risk would limit clinical use, and we would state it as such.