Separating Sampling Artifacts from Real Mechanism Differences in Multi-Cohort Causal Discovery

When several longitudinal studies of the same disease disagree about which symptom drives which, the usual explanation is that the studies differ: different patients, different settings, different mechanisms. There is a more mundane explanation that current methods cannot rule out. The studies observe the same process at very different time scales. A cohort measured every few weeks and a cohort measured once a year will recover different "lagged" causal graphs from identical underlying dynamics, because over a long interval an indirect path (A affects B, which affects C) looks like a direct edge from A to C. This proposal fits one continuous-time causal model jointly to all cohorts, each observed on its own schedule. It then asks which cross-cohort disagreements that model reproduces purely from the cohorts' different observation schedules. Disagreements it cannot reproduce are kept as genuine, cohort-specific mechanism differences, estimated as sparse deviations from a shared graph.

The motivating case is the five-cohort posttraumatic stress study of Pierce et al.. It ran a latent-confounder-aware search separately on each cohort and tallied the shared edges by hand. Follow-up ranged from 0–90 days (ADAPT) to 8 years (MYH), and secondary edges appeared in some cohorts and not others with no account of why. The claim here is that mismatched sampling is not only a nuisance. A densely sampled cohort pins down short-lag structure that a coarsely sampled cohort cannot resolve, while the coarse cohort tests long-horizon predictions. Mixed schedules therefore carry identifying information that separate analysis throws away. This mirrors how FedCDH turns client-level distribution shift into a signal for orienting edges, applied here to time rather than to static distributions.

Core Claim

Model cohort $m$'s variables $x(t)$ as a linear stochastic differential equation, a continuous-time analogue of vector autoregression:

$$dx = (A + D_m)\,x\,dt + \Sigma_m^{1/2}\,dW_t .$$

Here $A$ is a sparse drift matrix shared by all cohorts; its off-diagonal nonzeros are the causal graph. $D_m$ is a sparse cohort-specific deviation, $\Sigma_m$ is cohort noise covariance, and $W_t$ is Brownian noise. Between two observations separated by an interval $\Delta$, the exact transition matrix is $\exp((A+D_m)\Delta)$. The likelihood is therefore exact for any irregular schedule, with no interpolation. We estimate

$$\min_{A,\{D_m,\Sigma_m\}} \; -\sum_m \log p_m(\text{data}_m \mid A+D_m,\Sigma_m) + \lambda \lVert A\rVert_1 + \mu \sum_m \lVert D_m\rVert_{2,1},$$

where the group penalty $\lVert\cdot\rVert_{2,1}$ zeroes out whole rows of $D_m$, so a cohort deviates only where its data demand it.

The new analysis object is the sampling-explained disagreement. For each cohort, we take the fitted shared model with $D_m=0$ and push it through that cohort's actual observation schedule. We then check whether the implied discrete-time graph reproduces the edge differences that per-cohort discrete discovery finds. Disagreements reproduced this way are attributed to sampling. The rest are attributed to mechanism.

We start linear on purpose. CausalRivers found that linear vector autoregression was the most reliable established method on real river networks, and that nonlinear methods often failed to beat it. The aliasing argument is also cleanest when transitions are matrix exponentials. A nonlinear version replaces the drift with the neural-network vector field and first-layer group penalty of Bellot et al.'s neural graphical model, adding a cohort-specific deviation. It is an extension, not the headline.

Relation to Prior Work

Three lines of work supply ingredients, and each lacks one piece. Bellot et al. learn continuous-time causal structure that is consistent under irregular sampling, and they show discrete-time Granger methods suffer exploding false discoveries at sparse sampling. However, they assume a single homogeneous system. We reuse their continuous-time premise and add multiple cohorts. Meta-D2AG splits a temporal graph into a shared part and domain-specific parts through a Hadamard product. It assumes uniform discrete time steps, so its domain parts would absorb sampling-rate differences as if they were mechanism changes, which is the confusion we target. SPACETIME groups sites into discrete contexts sharing mechanisms by description length. It also works on a common discrete lag grid and scales poorly with the number of variables.

FedCDH motivates treating cohort identity as information, but it is static and has no notion of lag. Pierce et al. provides both the motivating disagreement and a constraint: it handles latent confounding, which our model does not. We treat that as a stated limitation and check it in simulation, rather than claiming to subsume their method.

Research Program

The work has three parts.

First, we build the estimator. It uses exact matrix-exponential likelihoods per observation interval, solved by proximal gradient with warm starts. The tuning parameters $\lambda,\mu$ are chosen by held-out log-likelihood on withheld participants per cohort.

Second, we formalize the attribution test. For each edge on which per-cohort discrete methods disagree, we compare two quantities by parametric bootstrap from the fitted model. One is the probability that the shared model at that cohort's schedule produces the edge. The other is the same probability under the model with the cohort's deviation included. This classifies each disagreement as sampling-explained, mechanism-explained, or unresolved.

Third, we characterize identifiability. With a single coarse interval, the matrix logarithm is non-unique, so $A$ is not identified. We will show, and check numerically, that combining cohorts with incommensurate intervals restores identifiability. This would make the "heterogeneity is information" claim precise.

Baselines

The naive reference point is the Pierce-style protocol. It runs a discrete-time method (vector autoregression, and GFCI where confounding matters) separately on each cohort at its native spacing, and reports edges present in a majority of cohorts. Every cross-cohort difference is read as real heterogeneity. Beating it means a lower structural Hamming distance (the number of wrong, missing or extra edges) to the true shared graph, and correct attribution of injected versus sampling-induced differences.

The strongest real-data competitor is pooled linear vector autoregression. Following CausalRivers, which reports AUROC of 0.80–0.85 for vector autoregression and CDMI on its Random and Close graph samples, we fit it with cohort-specific intercepts on a common resampled grid.

The strongest heterogeneity-aware method is Meta-D2AG, given cohort labels as known domains and data interpolated to a uniform grid. Its reported structural Hamming distance on Sprites World with 10 objects is 9.1, against 12.0 for IDYNO and 39.0 for DYNOTEARS. We will reproduce this on uniformly sampled Sprites World before using its subsampled variants, so any gain is measured against a correctly working implementation.

SPACETIME runs with cohorts supplied as candidate contexts, on problems small enough for its search. Pooled continuous-time fitting without deviations, which is our model with $D_m=0$, is both a baseline and the key ablation. A second ablation keeps $D_m$ but falsely assigns every cohort the same interval. It isolates whether exact per-cohort schedules, rather than the shared-plus-deviation structure, drive any gain.

All methods see identical participants and splits, get the same hyperparameter search budget (equal number of configurations, selected on the same held-out likelihood or validation split), and run on the same hardware with a common wall-clock cap.

Why not just…?

Why not just interpolate every cohort onto a common grid and run Meta-D2AG? Interpolating annual survey waves to weekly resolution invents data, and the smoothing itself creates spurious lagged dependence. Bellot et al. document the closely related failure of discrete methods under sparse sampling. This baseline is run directly. If it matches our model on the subsampled benchmarks below, the proposal's central claim fails.

Why not just meta-analyze per-cohort vector autoregression coefficients with a random-effects model? A lag coefficient estimated at a 90-day spacing and one estimated at a 1-year spacing are different quantities, entries of $\exp(A\Delta)$ at different $\Delta$. Averaging them assumes a common effect that does not exist even when mechanisms are identical. The file also notes that random-effects models assume normally scattered effects rather than structurally different graphs. Our identical-mechanism benchmark measures how much spurious "heterogeneity" this approach reports.

Why not just fit one pooled continuous-time model and ignore heterogeneity? This is the real threat. If cohorts truly share mechanisms, it may be as good as our model and simpler. That outcome would still be informative, since it would say the published disagreements are sampling artifacts. We test it in both regimes, with and without injected mechanism changes. The deviation terms must cost almost nothing in the first regime and be clearly better in the second.

Proposed Experiments

The decisive test uses CausalRivers, whose 15-minute river data come with physically derived ground-truth flow graphs. From RiversEastGermany and RiversBavaria subgraphs we create pseudo-cohorts. Each pseudo-cohort covers a different time window and is subsampled to a different schedule (dense short windows, sparse long windows, irregular gaps), mimicking the Pierce follow-up structure. Mechanisms are identical across pseudo-cohorts by construction, so every disagreement among per-cohort methods is a sampling artifact.

Success means three things. Our model attributes the large majority of those disagreements to sampling, keeps the deviations $D_m$ near zero, and matches or exceeds pooled vector autoregression's AUROC on the shared graph. We then add RiversElbeFlood periods as a cohort with plausibly altered dynamics, and check that its deviation terms activate there and not elsewhere.

On synthetic linear and nonlinear systems, including Rössler at $d=100$ where Bellot et al. report true positive rate above 0.95 for a single system, we inject known cohort-specific edge changes. We measure structural Hamming distance on $A$, recovery of $D_m$ support, and attribution accuracy. We also simulate hidden confounders to quantify how badly our sufficiency assumption fails relative to GFCI.

Subsampled Sprites World extends the head-to-head comparison against Meta-D2AG to irregular schedules.

We will request access to the five PTSD cohorts. If granted, the scientific question is whether the cohort-specific secondary edges in Pierce et al. survive once the follow-up mismatch is modeled. That study reports no numerical edge-stability values, so this analysis has no ground truth. It will be presented as exploratory, alongside a simulation calibrated to the cohort sizes (43 to 243) and schedules.