In this article, we use the definition of ‘causality’ that is common in statistics and intuitive to scientists: X has a causal effect on Y (‘X causes Y’ or ‘X is a causer; Y is a causee’ or ‘X is a cause; Y is an effect’) if some externally applied perturbation of X can result in a perturbation in Y (Figure 1A). We say that X and Y are causally related if X causes Y, Y causes X, or some other variable causes both. Otherwise, X and Y are causally unrelated. Additionally, one can talk about direct versus indirect causality (Figure 1B; see legend for definitions). A surprising result from past several decades of causality research is that there are in fact some conditions under which directional causal structures can be correctly inferred (‘identified’) from purely observational data (Spirtes and Zhang, 2016; Peters et al., 2017; Hitchcock, 2020b) (e.g. Appendix 2—figure 2, last row). However, empirical time series often do not contain enough information for easy causal identifiability (Spirtes and Zhang, 2016; Glymour et al., 2019).

The adage ‘correlation is not causality’ is well-known to the point of being cliché (Sugihara et al., 2012; Coenen and Weitz, 2018; Carr et al., 2019; Mainali et al., 2019). Yet, to dismiss correlative evidence altogether seems too extreme. To make use of correlative evidence without being reckless, it helps to distinguish between the terms ‘correlation’ and ‘dependence’. When applied to ecological time series, the term ‘correlation’ is often used to describe some statistic that quantifies the similarity between two observed time series (Weiss et al., 2016; Coenen and Weitz, 2018). Examples include Pearson’s correlation coefficient and local similarity (Ruan et al., 2006). In contrast, statistical dependence is a hypothesis about the probability distributions that produced those time series, and has close connections to causality.

Dependence has a precise definition in statistics, and is most easily described for two binary events. For instance, if the incidence of vision loss is higher among diabetics than among the general population, then vision loss and diabetes are statistically dependent. In general, events A and B are dependent if across many independent trials (e.g. patients), the probability that A occurs given that B has occurred (e.g. incidence of vision loss among diabetics only) is different from the background probability that A occurs (e.g. background incidence of vision loss). If A and B are not dependent, then they are called independent. The concept of dependence is readily generalized from binary events to numerical variables, and also to vectors such as time series (Appendix 1).

Dependence is connected to causation by the widely accepted ‘Common Cause Principle’: if two variables are dependent, then they are causally related (i.e. one causes the other, or both share a common cause; Peters et al., 2017; Runge et al., 2019a; Hitchcock, 2020b; Hitchcock and Rédei, 2020a). Note however that if one mistakenly introduces selection bias, then two independent variables can appear to be dependent (Appendix 2—figure 3). The closely related property of conditional dependence (i.e. whether two variables are dependent after statistically controlling for certain other variables; Appendix 1) can be even more causally informative. In fact, when conditional dependence (and conditional independence) relationships are known, it is sometimes possible to infer most or all of the direct causal relationships at play, even without manipulative experiments or temporal information. Many of the algorithms that accomplish this rely on two technical but often reasonable assumptions: the ‘causal Markov condition’, which allows one to infer causal information from conditional dependence, and the ‘causal faithfulness condition’, which allows one to infer causal information from conditional independence (Appendix 2; Peters et al., 2017; Glymour et al., 2019; Hitchcock, 2020b).

In sum, whereas a correlation is a statistical description of data, statistical dependence is a hypothesis about the relationship between the underlying probability distributions. Dependence is in turn linked to causality. Below, we discuss tests that use correlation to detect dependence in time series.

Despite its scientific usefulness, dependence between time series can be treacherous to test for. This is because time series are often autocorrelated (e.g. what occurs today influences what occurs tomorrow), so that a single pair of time series contains information from only a single trial. If one has many trials that are independent and free of systematic differences (e.g. ≥20 as in some laboratory microcosm experiments), the task is relatively easy: One can test whether the abundances of species X and Y are statistically dependent by comparing the correlation between X and Y abundance series from the same trial with those between X and Y abundance series from different trials (Appendix 1—figure 4; see also Moulder et al., 2018). However, a large trial number is generally a luxury and often only one trial is available. In such cases, attempting to discern whether two time series are statistically dependent is like attempting to divine whether diabetes and vision loss are dependent with only a single patient (i.e. we have an ‘n-of-one problem’). As one possible remedy, there are parametric tests using the Pearson correlation coefficient that account for autocorrelation. In these tests, one estimates the correlation coefficient between time series, and evaluates its statistical significance using the variance of the null distribution (Afyouni et al., 2019). However, the calculation of this variance relies on estimates of the autocorrelation at each lag for both time series, which can be highly uncertain (Pyper and Peterman, 1998; Ebisuzaki, 1997). Furthermore, after estimating the variance, one must also assume the shape of the null distribution before a p-value can be assigned to the correlation.

Alternatively, the n-of-one problem is often addressed by a technique called surrogate data testing. Specifically, one computes some measure of correlation between two time series X and Y. Next, one uses a computer to simulate replicates of Y that might have been obtained if X and Y were independent (see below). Each simulated replicate is called a ‘surrogate’ Y. Finally, one computes the correlation between X and each surrogate Y. A p-value (representing evidence against the null hypothesis that X and Y are independent) is then determined by counting how many of the surrogate Ys produce a correlation at least as strong as the real Y. For example, if we produced 19 surrogates and found the real correlation to be stronger than all 19 surrogate correlations, then we would write down a p-value of 1/(1+19)=0.05. Ideally, if two time series are independent, then we should register a a p-value of 0.05 (or less) in only 5% of cases.

Several procedures can be used to produce surrogate time series, each corresponding to an assumption about how the original time series was generated (Lancaster et al., 2018). One popular procedure is to simply shuffle the values of a time series (Ruan et al., 2006; Eiler et al., 2012; Shade et al., 2013; Cyriaque et al., 2020). This procedure, often called permutation, assumes that all possible orderings of the time points in the series are equally likely. This assumption is commonly violated in time series due to autocorrelation, and thus the test is often invalid. For example, for independent time series in Figure 2B–C, this test returns p<0.05 at rates of 30∼92%, much higher than 5%. Nevertheless, permutation testing has appeared in many applied works, perhaps because it has been the default option in some popular software packages. Another procedure for generating surrogates is called phase randomization. It first uses the Fourier transform to represent a time series as a sum of sine waves, then randomly shifts each of the component sine waves in time, and finally sums the phase-shifted components (Ebisuzaki, 1997; Schreiber and Schmitz, 2000; Andrzejak et al., 2003; Appendix 3—figure 1). This procedure is considered appropriate when the original time series is obtained from a linear, Gaussian, and stationary process (Andrzejak et al., 2003; Lancaster et al., 2018), where ‘linear’ means that future values depend linearly on past values, ‘Gaussian’ means that any subsequence follows a multivariate Gaussian distribution, and ‘stationary’ means that this distribution does not change over time. See Chan, 1997 for a discussion of exact requirements. Indeed, this test performed well (with a false positive rate of 4%) when time series satisfied its assumptions (Figure 2C), and poorly when the stationarity assumption was violated (with a false positive rate of 21%; Figure 2B). Other surrogate data procedures include time shifting (Andrzejak et al., 2003), the block bootstrap (Papana et al., 2017), and the twin method (Thiel et al., 2006). Some surrogate data tests have been shown to perform reasonably well even when the exact theoretical requirements are unmet or unknown (Thiel et al., 2006; Papana et al., 2017), but a more comprehensive benchmarking effort is needed to map out each method’s valid domain in practice.

In sum, surrogate data allow a researcher to use an observed correlation statistic to test for dependence under some assumption about the data-generating process. Dependence indicates the presence of a causal relationship, and conditional dependence can sometimes even indicate the direction (Hitchcock, 2020b; Glymour et al., 2019; Heinze-Deml et al., 2018; Appendix 2—figure 2). Below we consider Granger causality and state space reconstruction, two approaches that can be used to directly infer the direction of causality from time series.

In simple language, X is said to Granger-cause Y if a collection of time series containing all historical measurements predicts Y’s future behavior better than a similar collection that excludes the history of X. An important consequence of this definition is that Granger causality excludes indirect causes, as illustrated in Figure 3A. In practice, whether a causal relationship is direct or indirect depends on which variables are observed. For instance, in Figure 3A, if Y were not observed, then X would “directly” cause (and Granger-cause) Z.

Granger causality has many related but nonequivalent quantitative incarnations in the literature, including several that were proposed by Granger himself (Granger, 1969; Granger, 1980). Box 1 presents two definitions: one based on a linear regression which we call ‘linear Granger causality’ (Gibbons et al., 2017; Ai et al., 2019; Barraquand et al., 2020; Mainali et al., 2019) and another more general definition which we call ‘general Granger causality’ (also sometimes called nonlinear Granger causality; Granger, 1980; Diks and Panchenko, 2006; Bekiros and Diks, 2008; Vicente et al., 2011; Roux et al., 2013; Papana et al., 2017). See theorem 10.3 of Peters et al., 2017 for a discussion of the theoretical relationship between general Granger causality and (true) causality.

We discuss four important instances where Granger causality can fail as an indicator of direct causality (Figure 3B). These pathologies can be understood intuitively and can apply to both linear and general Granger causality. First, if a system has deterministic dynamics (see Appendix 3), then Granger causality may fail to detect causal relations (Figure 3Bi). More generally, if dynamics have a low degree of randomness, Granger causality signals can be very weak (e.g. knowing X’s past improves predictions of Y’s future only slightly; Janzing et al., 2013; Peters et al., 2017). Moreover, as we will discuss later, this limitation has motivated other methods that take a primarily deterministic view (Sugihara et al., 2012). Second, Granger causality may erroneously assign a direct causal relation between a pair of variables that have an unobserved common cause (Figure 3Bii). Third, recording data at a frequency below that of the original process by ‘subsampling’ (e.g. taking weekly measurements of a daily process) or by ‘temporal aggregation’ (e.g. taking weekly averages of a daily process) can alter the inferred causal structure (Figure 3Biii), although recent techniques can help with these issues (Gong et al., 2015; Hyttinen et al., 2016; Gong et al., 2017). Lastly, when measurements are noisy (Figure 3Biv), Granger causality can assign false interactions and also fail to detect true causality (Newbold, 1978), although some progress has been made on this front (Nalatore et al., 2007).

One might still attempt to infer Granger causality despite the above caveats, especially in situations where caveats can be largely avoided. Linear Granger causality has standard parametric tests: if any of the αk terms in Equation 1 is nonzero, then X linearly Granger-causes Y. Parametric tests are computationally inexpensive and available in multiple free and well-documented software packages (Seabold and Perktold, 2010; Barnett and Seth, 2014). These tests assume that time series are ‘covariance-stationary’, which means that certain statistical properties of the series are time-independent (Barnett and Seth, 2014; see also Appendix 3), and can fail when this assumption is violated (Toda and Phillips, 1993; Ohanian, 1988; He and Maekawa, 2001). Additionally, applying linear Granger causality to nonlinear systems can lead to incorrect causal conclusions (Li et al., 2018). One can assess whether the linear model (Equation 1) is a reasonable approximation, for instance by checking whether the model residuals εt are uncorrelated across time (Feige and Pearce, 1979) as is assumed by Equation 1.

Tests for general Granger causality often use a statistic known as transfer entropy (Papana et al., 2012). Roughly, the transfer entropy from X to Y is the extent to which the entropy (a measurement of uncertainty) of Y’s future is reduced when we account for (specifically, condition on) the past of X (Schreiber, 2000; Cover and Thomas, 2006; Montalto et al., 2014; Papana et al., 2017). A significant transfer entropy thus indicates the presence of general Granger causality. Surrogate data are typically used to evaluate significance (Montalto et al., 2014; Papana et al., 2017; Shorten et al., 2021). However, the previously discussed surrogate data procedures are designed to test the null hypothesis of independence, which is different from the null hypothesis of general Granger non-causality (i.e. Equation 2, but replace ‘≠’ with ‘=’). More recent surrogate procedures have been proposed to address this issue (Runge, 2018a; Shorten et al., 2021). Several software implementations of Granger causality tests based on transfer entropy statistics are available (e.g. Montalto et al., 2014; Behrendt et al., 2019; Wollstadt et al., 2019).

Granger causality methods face challenges when datasets have a large number of variables (e.g. in microbial ecology). In this case, the summation in Equation 1 will contain a large number of terms, and so a regression procedure may fail to detect many true interactions (Runge et al., 2019a; Runge et al., 2019b). To handle systems with many variables, one can impose the assumption that only a small number of causal links exist (Gibbons et al., 2017; Mainali et al., 2019). This is sometimes called sparse regression or regularization. Additionally, under certain technical assumptions, it is possible to use a series of logical rules to remove unnecessary terms in a purely data-driven way (Runge et al., 2019b; Runge et al., 2019a). As an example, suppose that we wish to test whether pH is a Granger-cause of chlorophyll concentration in some aquatic environment and we infer based on a prior analysis that chlorophyll concentration is always independent of fluctuations in salinity. Then, most likely, salinity is irrelevant to the pH-chlorophyll relationship and can be safely omitted from our Granger causality analysis. As an aside, this reasoning could theoretically fail in pathological cases where, for instance, the ‘faithfulness’ condition (Appendix 2) is violated (see Example 7 of Runge, 2018b for a worked counterexample). These rules and their associated assumptions are formalized in ‘constraint-based’ causal discovery algorithms (Appendix 2; Peters et al., 2017; Glymour et al., 2019). The development of new causal discovery algorithms, and their application to time series, is a very active area of research (Hyvärinen et al., 2010; Runge et al., 2019b; Runge et al., 2019a; Sanchez-Romero et al., 2019).

Consider the deterministic dynamical system in Figure 4. Here, Z is causally driven by X and Y, but not by W or V. We can make a vector out of the current value Z⁢(t) and two past values Z⁢(t-τ) and Z⁢(t-2⁢τ), where τ is the time delay and [Z⁢(t),Z⁢(t-τ),Z⁢(t-2⁢τ)] is called a ‘delay vector’ (Figure 4B, red dots). The delay vector can be represented as a single point in the three-dimensional Z ‘delay space’ (Figure 4C, red dot). We then shade each point of the trajectory in Z delay space according to the contemporaneous value of Y, which causally influences Z. Since in this example each point of the trajectory in Z delay space corresponds to one and only one Y⁢(t) value, we call this a ‘delay map’ from Z to Y. Notice that the Y⁢(t) gradient in this plot looks gradual in the sense that if two points are nearby in the delay space of Z, then their corresponding Y⁢(t) shades are also similar. This property is called ‘continuity’ (Appendix 4—figure 1). Overall, there is a continuous map from the Z delay space to Y, or more concisely, a ‘continuous delay map’ from Z to Y. A similar continuous delay map also exists from Z to its other causer X. On the other hand, if we shade the delay space of Z by W or V (neither of which causes Z), we do not get a continuous delay map (Figure 4D–E).

In this example, there is a continuous delay map from a causee to a causer, but not the other way around, and also no continuous delay map between causally unrelated variables. If this behavior reflects a broader principle, then perhaps continuous delay maps can be used to infer the presence and direction of causation. Is there in fact a broader principle?

In fact, there is a sort of broader principle, but it may not be fully satisfying for causality testing. The principle stems from a classic theorem due to Takens, 1980. A rough translation of Takens’ theorem is the following: If a particle follows a deterministic trajectory which forms a surface (e.g. an ant crawling all over a doughnut), and if we take one-dimensional measurements of that particle’s position over time (e.g. the distance from the ant’s starting position), then we are almost guaranteed to find a continuous delay map from our measurements (of current distance) to the original surface (the donut), as long as we use enough delays. (We walk through visual examples of these ideas in detail in Appendix 4.) A key result that follows from this theorem is that we can typically (‘generically’) expect to find continuous delay maps from ‘dynamically driven’ variables to ‘dynamically driving’ variables in a coupled deterministic dynamical system, as long as certain technical requirements are met (Cummins et al., 2015). Although the notion of ‘dynamic driving’ (Cummins et al., 2015) differs from our definition of causation, the two are related and we will still use the standard notion of causation when evaluating the performance of SSR methods. In theory, Takens’ theorem says that almost any choice of delay vector should work as long as it contains enough delays. However in practice, with finite noisy data, the behavior of SSR methods can depend on the delay vector selection procedure (Cobey and Baskerville, 2016; see also Appendix 4). Overall, Takens’ theorem and later results (Sauer et al., 1991; Cummins et al., 2015) form the theoretical basis of SSR techniques.

SSR techniques attempt to detect a continuous delay map (or a related feature) between two variables and use this to infer the presence and direction of causation (Sugihara et al., 2012; Ma et al., 2014; Harnack et al., 2017): A continuous delay map from Y to X is taken as an indication that X causes Y. The fact that the map points in the opposite direction as the expected causation is potentially counterintuitive. One informal explanation is that the delay vectors of the causee can contain a record of past influence from the causer (Sugihara et al., 2012). As a word of warning, while causation is one possible explanation for a continuous delay map, it is not the only possible explanation. Indeed, we now illustrate scenarios where a causal relationship and a continuous delay map do not coincide.

Figure 5 illustrates four failure modes of SSR. In the first failure mode, which we refer to as ‘nonreverting continuous dynamics’ (top row of Figure 5; see also Appendix 4), a continuous map arises from the delay space of X to Z because a continuous map can be found from the delay space of X to time (‘nonreverting X’) and from time to Z (‘continuous Z’). This pathology leads to false causal conclusions and may explain apparently causal results in some early works where SSR methods were applied to data with a clear temporal trend. We are not aware of statistical tests for this problem, but Clark et al., 2015 recommend shading points in the delay space with their corresponding time to visually check for a time trend. In the second failure mode (Figure 5, second row; see also Sugihara et al., 2012), one variable drives another variable in such a way that the dynamics of the two variables are synchronized. Consequently, although the true causal relationship is unidirectional, bidirectional causality is inferred. Although the ‘prediction lag test’ (Figure 6B right panel) can sometimes alleviate this problem (Ye et al., 2015; Cobey and Baskerville, 2016), it is not foolproof as we demonstrate in Appendix 4. In the third failure mode (Figure 5 third row), X and Z both oscillate and X’s period is an integer multiple of Z’s period. In this case, Z is inferred to cause X even though they are causally unrelated (see also Cobey and Baskerville, 2016). In the fourth failure mode (Figure 5, bottom row), SSR gives a false negative error due to ‘pathological symmetry’, although this may be rare in practice.

SSR causal discovery methods require testing for the existence of continuous delay maps between variables. However, testing for continuity in real data is complicated by noise and discrete sampling (Figure 4, compare panels C and F; see also Appendix 4—figure 1).

Several methods have been used to detect SSR causal signals by detecting approximate continuity (Cummins et al., 2015) or related properties (Sugihara et al., 2012; Ma et al., 2014; Harnack et al., 2017). The most popular is convergent cross mapping (CCM), which has been applied to nonlinear (Sugihara et al., 2012) or linear deterministic systems (Barraquand et al., 2020). CCM is based on a statistic called ‘cross map skill’ that quantifies how well a causer can be predicted from delay vectors of its causee (Figure 6A), conceptually similar to checking for gradual transitions when shading the causee delay space by causer values (Figure 4). Four criteria have been proposed to infer causality (Sugihara et al., 2012; Ye et al., 2015; Cobey and Baskerville, 2016; Figure 6B): First, the cross map skill must be positive. Second, the cross map skill must be significant according to some surrogate data test. Third, the cross map skill must increase with an increasing amount of training data. Lastly, the cross map skill must be greater when predicting past values of the causer than when predicting future values of the causer (the prediction lag test [Ye et al., 2015; Cobey and Baskerville, 2016] in the right panel of Figure 6B, but see Appendix 4 for caveats of this test). In practice, many if not most CCM analyses use only a subset of these four criteria (Sugihara et al., 2012; Brookshire and Weaver, 2015; Cramer et al., 2017; Wang et al., 2018). Other approaches to detect various aspects of continuous delay maps have also been proposed (Ma et al., 2014; Cummins et al., 2015; Harnack et al., 2017; Leng et al., 2020). We do not know of a systematic comparison of these alternatives.