Convergent cross mapping (CCM) is a way to detect causation in nonlinear dynamical systems such as ecosystems, physiology, and climate. Ordinary regression and its predictive variant, Granger causality, can miss these links or invent them. The test rests on one idea: if $X$ drives $Y$, the history of $Y$ carries a trace of $X$. Nearby points in the reconstructed state of $Y$ then let you estimate $X$, and the estimate improves as you collect more data. That last requirement, called convergence, needs long and stationary records from a single system. Clinical and biological data rarely look like that. They arrive as many short series from different studies, hospitals, or labs. Each source admits patients under its own diagnostic threshold, calibrates monitors differently, and may intervene on the system in its own way. Pooling these series naively mixes several attractors (the geometric shapes a system's trajectories settle onto) into one tangled cloud. Analyzing each study separately often leaves too little data per study to show convergence at all.
This note proposes to use the studies themselves as the unit of convergence. The core test is "transported cross mapping." To check whether the coupling $X \to Y$ is shared across studies, we estimate $X$ in a held-out study using only nearest neighbors found in the other studies' reconstructions of $Y$. This works after a per-study recalibration fitted without ever looking at $X$. If the coupling law is shared, skill should rise as more studies are added, even when no single study is long enough to converge by itself. If transport fails for one particular study while it succeeds elsewhere, that study has probably intervened on or altered that link. The method thus turns study heterogeneity from a nuisance into evidence, which is the stance InvarGC takes for Granger causality, but carried over to non-separable dynamics.
Core Claim
The causal content of cross mapping is the existence of a smooth map from the reconstructed state of $Y$ to the value of $X$. A shared physical coupling implies that this map is approximately the same in every study, even when the studies sample different regions of state space or run under different parameters. Study-level heterogeneity of two kinds leaves such a map intact. Selection-type heterogeneity, such as different severity thresholds at admission, only changes which part of the attractor a study visits. Observation-type heterogeneity, such as calibration offsets or different sampling rates, is an invertible distortion of the coordinates, so it can be undone. A third kind, genuine changes to the coupling in some study, does break the map, and transport should detect exactly that.
Write $M_Y^{(s)}$ for the delay-coordinate reconstruction of $Y$ in study $s$, built from lagged copies of $Y$ after study-specific recalibration $g_s$. The transported skill for held-out study $s$ is
$$\rho_s(L, K) = \mathrm{corr}\big(X^{(s)}(t),\ \hat X^{(s)}(t) \mid \textstyle\bigcup_{k \in \mathcal{K}} M_Y^{(k)}\big),$$
where $\mathcal{K}$ is a random set of $K$ other studies and $L$ is the library length taken from each. The causal claim is that $\rho_s$ increases in the total library $KL$ and plateaus at a positive value. The reverse direction and spurious "mirage" correlations from shared seasonal rhythms should fail to show this. The invariance claim is separate: a study whose plateau falls well below the leave-one-out distribution of the others is flagged as having a study-specific coupling.
One design rule carries most of the weight. The recalibrations $g_s$, and any learned alignment of the reconstructions, are fitted only to make $Y$ predict its own future across studies. They never use $X$. Fitting the alignment to maximize cross-map skill would manufacture causality, and one of the ablations below exists to show how large that leakage effect is.
Relation to Prior Work
The method comes from the CCM line. Reviews by Ma et al. and Runge et al. explain why non-separable systems defeat regression and Granger tests. They also show that CCM assumes one autonomous, stationary attractor, and that assumption is exactly what multi-study data violate. Three extensions make the single-system estimator more robust, and all three still assume one system. Latent CCM replaces delay vectors with a continuous-time latent state learned by a neural ordinary differential equation, which handles sporadic sampling. Tangent Space Causal Inference compares velocity vectors instead of point predictions, which resists synchrony failures. TopoDistill distills a denoised neighborhood structure from a multivariate teacher model. We reuse delay embedding and, as one variant, the latent embedding of Latent CCM as building blocks. The new part is the cross-study convergence axis and the transport test, which none of the three defines.
InvarGC motivates the proposal and sets its competitive bar. It shows that multiple environments can separate invariant causal edges from environment-specific interventions. Its identifiability results, however, are linear and Granger-based, and so rely on the separability assumption that Butler et al. argue fails in coupled dynamics. Our proposal makes the same structural move with state-space geometry in place of predictive separability.
The finding of Jiang et al. that noise can make directed influence easier to detect, by pushing trajectories off degenerate orbits, suggests a hypothesis we will test: parameter diversity across studies may help in the same way, because together the studies cover more of state space than any one does.
The heterogeneity literature supplies the regime. Clinical cohorts differ in diagnostic thresholds and endpoint definitions, as with the inconsistent mortality and length-of-stay targets documented by PyHealth. Standard meta-analytic models, such as the bivariate mixed models, treat study differences as Gaussian random effects on static quantities. We use PyHealth for cohort parsing. We do not claim to solve outcome-definition heterogeneity. Transport assumes $X$ means the same thing in every study, and studies with incompatible endpoint definitions are out of scope.
Research Program
We will build the estimator in three layers. The first layer is per-study recalibration. Each $g_s$ is a monotone transform with optional resampling to a common time step. It is chosen to minimize cross-study self-forecast error of $Y$, meaning that neighbors in other studies' reconstructions should predict the next value of $Y$ in study $s$. Embedding dimension and delay are chosen the same way, again with no access to $X$.
The second layer is the transported skill curve. We compute $\rho_s(L, K)$ over a grid of library length $L$ and number of source studies $K$, using simplex-style nearest-neighbor estimation. We also run a delay-free variant in which each study's reconstruction is the latent state of a shared Latent CCM encoder trained without $X$.
The third layer is inference. Convergence is tested with a block bootstrap over studies, which gives a confidence band on the slope and plateau of $\rho$ against $KL$. Edge-level study shifts are flagged when study $s$'s plateau falls outside the leave-one-study-out distribution. A permutation null, which shuffles the pairing of $X$ and $Y$ series across studies, guards against shared rhythms such as circadian or seasonal cycles.
The analysis then asks two questions. The first is where the crossover lies between transported cross mapping and simply running CCM in each study, as a function of per-study length. The second is whether between-study parameter diversity helps or hurts detection under strong coupling, where single-study CCM is known to give two-way false positives.
Baselines
The naive reference point is concatenated CCM. All studies' series are standardized and joined into one library, and ordinary CCM is run on it. This is what an analyst would do by default. Prior evidence suggests it breaks on fragmented data: in Latent CCM, multi-spatial CCM "performed poorly or failed entirely" on sporadic double-pendulum data, where Latent CCM reached AUC 1.0. We run it with the same embedding choices and the same data.
The strongest simple competitor is per-study CCM with meta-analysis. CCM is run separately in each study. Each study's convergence slope and plateau are summarized, and the summaries are pooled with a random-effects model, with study-specific shifts flagged by heterogeneity diagnostics. It is the obvious statistician's answer to our question and needs no new machinery. It gets the same embedding search and bootstrap budget.
The strongest existing method for multi-environment causal discovery is InvarGC. It reports AUROC 0.8121 on the confounded Tennessee Eastman Process benchmark (Conf-TEP), against 0.7503 for eSRU, and AUPRC 0.9341 on the Causal Rivers confounder subset, against 0.8691 for CUTS. We run its released configuration on identical splits, with the same per-environment data. Beating it means a higher AUROC on Conf-TEP than the reported 0.8121, and higher AUROC on our nonlinear multi-study simulations, where it should be most exposed. We will also report where it wins.
We include two single-system dynamical estimators applied to pooled data. One is TSCI, which reports a correlation score of 0.915 on the double pendulum against 0.737 for Latent CCM. The other is Latent CCM with a study indicator added to its input. All neural baselines get the same hyperparameter search budget as our latent variant.
Two ablations isolate the key ingredients. The first removes recalibration, so transport runs on raw standardized series. The second fits recalibration to maximize cross-map skill on $X$. This leakage ablation should raise skill in both directions and inflate false positives, which would confirm that the self-forecast restriction matters. No reported result found on Lacuna for any CCM-family method on Conf-TEP or on multi-study clinical series, so those comparisons will be new numbers.
Why not just…?
Why not just run CCM in each study and meta-analyze? This is the real threat. When every study is long enough to converge by itself, we expect it to match transported cross mapping, and we will say so. Our claim is limited to the regime where per-study libraries are too short to converge but the pooled library is not. The decisive experiment sweeps per-study length at a fixed total amount of data. If meta-analysis matches transport at every length, the contribution shrinks to the study-shift flagging. In that case we would reframe the work as a diagnostic tool rather than a more powerful estimator.
Why not just concatenate everything, or feed a study indicator into Latent CCM? Concatenation mixes attractors that differ in scale and parameters. The Latent CCM paper's own multi-spatial CCM result shows fragmentation alone is already damaging. A study indicator gives the encoder a free channel to memorize each study. That can absorb exactly the coupling differences we want to detect, and nothing in the model tests whether the cross map is shared. The pooled-baseline comparison measures both effects directly.
Why not just use InvarGC, perhaps with a nonlinear predictor? InvarGC's invariance reasoning is sound, but it asks whether $X$'s past adds predictive information about $Y$. Under strong coupling, $Y$'s own history already encodes $X$, so that question can return the wrong answer (Butler et al.). On linear or weakly coupled data, InvarGC should win, and we expect it may on Conf-TEP. The coupling-strength sweep in our simulations will show where the two approaches change places.
Why not just a mixed-effects regression with study random effects? Coupled variables can have near-zero linear association (Ma et al.), and a random intercept cannot distinguish a mirage correlation driven by a shared rhythm from real coupling. We include it as a sanity row on the simulated data only.
Proposed Experiments
The main testbed is synthetic multi-study data with known ground truth. We generate 5 to 40 "studies" of coupled Rössler–Lorenz and double-pendulum systems. Each study has its own parameters, admission-style selection into regions of state space, a monotone observation distortion, and resampling. Some studies receive an edge-level intervention that removes or reverses coupling. We vary per-study length, coupling strength (including the generalized-synchrony regime), and the size of the parameter spread. We report three metrics: AUROC for direction detection, the false-positive rate in the reverse direction, and AUROC for flagging the intervened studies.
A second testbed uses the NEST spiking-network simulator from Latent CCM to create several simulated "labs" with different recording sparsity. The external benchmarks are Conf-TEP and Causal Rivers, comparing against InvarGC's reported numbers under its environment splits. The clinical plausibility study uses eICU hospitals as studies, parsed with PyHealth, with MIMIC-IV held out. It uses a positive control with a known direction, vasopressor dose to mean arterial pressure, and negative controls built from series pairs taken from different patients. It is reported as plausibility evidence, not ground truth.
Three outcomes would decide whether the idea holds. First, transported skill should converge in total library size $KL$ for true directions while per-study CCM at the same per-study length does not. Second, the intervened studies should be flagged at better than chance. Third, the leakage ablation should visibly inflate false positives. If parameter diversity across studies reduces two-way false positives under strong coupling, that is a separate finding worth reporting on its own. If it increases them, that sets a limit on when transport can be trusted.
References
- InvarGC: Invariant Granger Causality for Heterogeneous Interventional Time Series under Latent Confounding
- Data-based prediction and causality inference of nonlinear dynamics
- Inferring causation from time series in Earth system sciences
- Latent Convergent Cross Mapping
- Tangent Space Causal Inference: Leveraging Vector Fields for Causal Discovery in Dynamical Systems
- TopoDistill: Distilling Global System Topology for Causal Discovery in Multivariate Time Series
- Directed dynamical influence is more detectable with noise
- PyHealth: A Deep Learning Toolkit for Healthcare Applications
- Is OR “portable” in meta-analysis? Time to consider bivariate generalized linear mixed model