Causal Caution in Causal Inference

• Causal Caution is defined as the disciplined practice of withholding causal claims when evidence is limited to correlations, emphasizing the need for robust intervention semantics and model adequacy.
• It highlights that methods like structural causal modeling, mediation analysis, and survival analysis require strong identifiability assumptions to make justified causal inferences.
• The approach advocates using interval estimates and detailed assumptions to prevent overconfident conclusions that may arise from model misspecification or inappropriate conditioning.

Causal Caution denotes the propensity to refrain from causal judgment when the evidence only shows correlation and is insufficient for causal inference, and to state explicitly why the inference is not warranted (Okumura, 23 Jun 2026). Across structural causal modeling, epidemiology, mediation analysis, missing-data theory, survival analysis, finance, dynamical systems, and AI, the same theme recurs: causal claims are only as strong as the intervention semantics, identifiability assumptions, model adequacy, and data support that justify them (Lemberger et al., 2020). Taken together, these works suggest that Causal Caution is not a rejection of causal inquiry, but a disciplined stance toward when causal effects are identified, when they are only bounded, and when apparently precise answers are artifacts of simplification, misspecification, or inappropriate conditioning.

1. Foundations: intervention, model dependence, and the difference between observation and action

A central premise of modern causal inference is that statistics alone can describe association, but not causation (Lemberger et al., 2020). Standard probability can express quantities such as $p(B \mid A)$, but causal questions require interventions, formalized by the do-operator. In a structural causal model, an intervention $do(X_i=a)$ replaces the structural equation for $X_i$ by $X_i=a$, and the post-intervention distribution is denoted $p(x\mid do(x_i=a))$; crucially,

$p(y\mid do(x_i=a)) \neq p(y\mid x_i=a)$

in general (Lemberger et al., 2020). This distinction underwrites the back-door criterion, the front-door criterion, and do-calculus, all of which are procedures for determining whether an interventional quantity can be expressed in terms of observed quantities and a causal graph (Lemberger et al., 2020).

The same literature also emphasizes that causal conclusions are model-relative. In structural-equation accounts of actual causation, the structural equations encode the effects of interventions, but the choice of variables, their ranges, and the inclusion of defaults or normality information can change causal verdicts (Halpern et al., 2011). The Halpern-Pearl framework makes this explicit: actual causation is evaluated within a model, and richer models may be needed to distinguish overdetermination from preemption, or ordinary from abnormal contingencies (Halpern et al., 2011). This implies that Causal Caution begins before estimation: it begins with the representation of the problem.

This suggests that causal rigor is inseparable from model specification. A graph, an estimand, and a set of intervention semantics are not merely notational choices; they determine what can be asked, what can be identified, and what should remain undecided.

2. Partial identification: why many causal questions support bounds rather than point estimates

In “causes of effects” problems, causal conclusions from statistical data are fundamentally limited (Dawid et al., 2017). For binary exposure $E$ and outcome $R$, the event that the exposure caused the outcome for an individual is represented as

$EC:\quad R_1=1,\; R_0=0,$

and the probability of causation is

$PC = (R_0=0 \mid E=1, R_1=1).$

Even under no confounding, one can usually identify only the marginal distributions of $do(X_i=a)$0 and $do(X_i=a)$1, not their joint distribution, so $do(X_i=a)$2 is generally not point-identified (Dawid et al., 2017). The basic bound is

$do(X_i=a)$3

where

$do(X_i=a)$4

The same caution appears in analyses of biased data, where omitted covariates or mediators can make bounds materially wrong; the paper’s examples show that ignoring a confounder can reverse the substantive conclusion, not merely make it slightly imprecise (Musio et al., 2023).

Additional structure can tighten bounds, but not automatically. Covariates, sufficient covariates, complete mediators, and partial mediators can refine the interval for $do(X_i=a)$5, yet the literature is explicit that more structure helps only when it genuinely carries identifying information (Dawid et al., 2017). In one example, mediator information tightened the bounds from $do(X_i=a)$6 to $do(X_i=a)$7; in other settings, adding a mediator does not always improve the bound (Dawid et al., 2017).

A related response to unmeasured confounding is the “Witness Protection Program” (WPP), which replaces sharp identification by bounds on the average causal effect via a linear programming approach and Bayesian inference (Silva et al., 2014). WPP uses observational conditional independencies to suggest weak paths in an unknown causal graph, relaxes faithfulness to allow varying degrees of path cancellations, and returns a posterior distribution over bounds on the average causal effect rather than a point estimate (Silva et al., 2014). This is a paradigmatic instance of Causal Caution: if the graph is weakly supported and confounding may remain, the honest output is a range with explicit assumptions.

Taken together, these results imply that interval-valued judgment is often not a concession but the correct inferential form. In such settings, overconfident point attribution is not just aggressive; it is formally unsupported.

3. Misspecification, aggregation, and counterfactual instability

A major source of causal overreach is the use of simplified or aggregated representations that do not preserve the causal question of interest. In longitudinal epidemiology, when a genuinely longitudinal causal process is collapsed into a simplified one-time-point or summary-based model, the quantity routinely estimated in practice is usually not the causal effect people think it is (Etievant et al., 2018). Under restrictive conditions, the simplified estimand can be written as a weighted average of longitudinal causal effects,

$do(X_i=a)$8

but these sufficient conditions are very restrictive, and the paper states that the quantities estimated in practice should be interpreted with caution in general, as they usually do not relate to any longitudinal causal effect of interest (Etievant et al., 2018).

An analogous warning appears in bulk transcriptomics. Aggregation is a lossy, non-invertible coarsening of the underlying cellular system, and causal relations are preserved only under linear aggregations coupled with affine structural equations (Luo et al., 30 May 2026). For additive noise models, if $do(X_i=a)$9, then under non-degenerate linear aggregation, functional-form consistency is preserved only if

$X_i$0

For post-nonlinear models, both $X_i$1 and $X_i$2 must be affine (Luo et al., 30 May 2026). Empirical analyses of four bulk and four single-cell datasets further reveal that the estimated pairwise regulatory functions among genes deviate from linearity in both data types, providing limited empirical support for the linearity assumptions required for recoverability (Luo et al., 30 May 2026).

Counterfactual analysis in dynamical systems introduces a different, but related, instability. In state-space SCMs,

$X_i$3

the standard abduction–action–prediction pipeline can fail badly when there are hidden states, observational noise, process noise, uncertain parameters, and especially chaotic dynamics (Aalaila et al., 31 Mar 2025). The paper’s most concise warning is that good factual fit does not imply reliable counterfactuals (Aalaila et al., 31 Mar 2025). In Lorenz and Rössler systems, generated counterfactuals can diverge strongly over time even with true parameters; parameter uncertainty and noise worsen the divergence (Aalaila et al., 31 Mar 2025).

Financial event studies provide a further example of model dependence. Traditional abnormal-return estimators are consistent only if the factor model is correctly specified; otherwise they converge to the wrong object (Goldsmith-Pinkham et al., 19 Nov 2025). Under misspecification,

$X_i$4

and the paper concludes that traditional methods remain reliable for short-horizon studies with random event timing, but caution is warranted when interpreting long-horizon or volatile-period event studies (Goldsmith-Pinkham et al., 19 Nov 2025).

These examples support a common lesson: representation can destroy identifiability. Aggregation, summary variables, unstable dynamics, and misspecified counterfactual benchmarks can produce estimands that are interpretable only under narrow structural regimes.

4. Time-to-event inference: hazard fragility, acceleration factors, and self-matched designs

In survival analysis, Causal Caution often centers on the choice of estimand. The hazard ratio for exposure has a complex causal interpretation in the presence of unmeasured heterogeneity, because hazards condition on being event-free at time $X_i$5, which induces built-in selection bias over time (Brathovde et al., 2024). To address this, a structural causal model for accelerated failure time (AFT) outcomes introduces frailty $X_i$6, treatment-effect heterogeneity $X_i$7, and idiosyncratic noise:

$X_i$8

The causal acceleration factor is

$X_i$9

Under no confounding and independent censoring, the observed acceleration factor equals the causal acceleration factor even with frailty and treatment heterogeneity, and with right-censored data it remains identifiable via Kaplan–Meier survival functions (Brathovde et al., 2024). The paper’s cautionary message is narrower: acceleration factors are attractive causal estimands, but estimation and interpretation under heterogeneity require caution because a time-varying observed acceleration factor may reflect unmeasured effect heterogeneity rather than a truly time-varying homogeneous treatment effect (Brathovde et al., 2024).

The case-crossover design illustrates a related asymmetry between null testing and point estimation. Once the design is placed in a formal counterfactual framework, the authors show that it is much safer for testing a null effect than for estimating a non-null causal effect (Shahn et al., 2020). Under strong assumptions, the estimator converges to

$X_i=a$0

where $X_i=a$1 is the desired causal hazard ratio and $X_i=a$2 is a bias factor (Shahn et al., 2020). When the treatment effect is non-null, there is a previously unnoticed bias arising from common causes of the outcome at different person-times; under some simplifying conditions, the bias is away from the null, but with correlated exposure histories the direction can go toward or away from the null (Shahn et al., 2020). The paper’s practical conclusion is explicit: the case-crossover design can be useful for testing the causal null hypothesis in the presence of baseline confounders, but extra caution is warranted when using the case-crossover design for point estimation of causal effects (Shahn et al., 2020).

These survival and event-time results reinforce a general principle: causal interpretation depends not only on whether an effect is estimated, but on whether the chosen time-scale and conditioning structure preserve a stable counterfactual contrast.

5. Mediation, missingness, and translational practice in epidemiology and medicine

Mediation analysis is not one problem but many different causal questions, and each question comes with its own identification logic (Nguyen et al., 2020). The literature organizes this complexity around five potential outcome types and three core assumption families—consistency, conditional independence, and positivity—and shows that the assumptions required differ across total effects, controlled direct effects, generalized direct effects, interventional effects, and natural effects (Nguyen et al., 2020). For example, the total effect is

$X_i=a$3

while a controlled direct effect is

$X_i=a$4

and natural effects require the cross-world quantity $X_i=a$5 (Nguyen et al., 2020). The paper’s central caution is that applied researchers should not assume that the assumptions for one mediation estimand automatically justify another; in the presence of intermediate confounders, natural effects are generally not identified, whereas interventional effects may still be (Nguyen et al., 2020).

In principal stratification with missing outcomes, the same caution applies to missingness assumptions. Latent ignorability or latent missing-at-random (LMAR),

$X_i=a$6

is often treated as a relaxation of MAR, but the graph-based analysis shows the opposite: LMAR is harder to satisfy than MAR, and for the purpose of breaking the dependence between the outcome and its missingness, no benefit is gained from conditioning on principal stratum on top of conditioning on observed variables (Nguyen, 2024). In some causal structures, conditioning on $X_i=a$7 can even make things worse by inducing collider bias (Nguyen, 2024). The recommendation is categorical: MAR should be preferred over LMAR (Nguyen, 2024).

Clinical translation of causal machine learning imports these same concerns into personalized treatment prediction. Causal ML differs from predictive ML because it targets potential outcomes $X_i=a$8, average treatment effects, conditional average treatment effects, and individualized treatment effects rather than prognosis alone (Feuerriegel et al., 2024). But caution is needed to avoid biased or incorrect predictions, especially when unconfoundedness is difficult to verify, overlap is weak, or uncertainty is not quantified (Feuerriegel et al., 2024). The recommended workflow is to define the research question, specify the causal graph, determine the data type, choose the causal estimand, check identifiability assumptions, select a causal ML method, quantify uncertainty, evaluate and validate, and report transparently (Feuerriegel et al., 2024). In this literature, Causal Caution takes the form of causal humility: stronger personalization requires stronger evidence.

Pandemic inference offers a further illustration. In estimating the effect of social mobility on Covid-19 deaths, the data support the idea that reduced mobility causes reduced deaths, but the conclusion comes with caveats (Bonvini et al., 2021). The authors emphasize time-varying confounding, unobserved infections, model misspecification, unmeasured confounding, limited data, and the null paradox (Bonvini et al., 2021). Here the causal signal is not denied; rather, the magnitude is treated as sensitive to the assumptions needed to identify it.

6. Human and machine expressions of causal caution

Causal Caution has also been operationalized as an observable behavior in AI systems. In LLMs used for decision support, a response is considered to manifest Causal Caution only if it includes explicit acknowledgment that the evidence is insufficient to assert causation, identification of concrete obstacles to causal inference such as confounding, reverse causation, selection bias, measurement bias, or lack of a control group, and suggestions for additional verification such as intervention experiments, natural experiments, identification strategies, or randomized comparisons (Okumura, 23 Jun 2026). Using a 4-level rubric inspired by Pearl’s Causal Hierarchy, the threshold is

$X_i=a$9

Across 480 trials, maintenance rates were 91.7–100.0% in academic contexts but dropped to 6.7–18.3% in practical advisory contexts; when restricted to practical prompts requesting concrete recommendations or explanatory rationales, only 1 of 200 responses (0.5%) maintained Causal Caution (Okumura, 23 Jun 2026). A brief self-correction prompt restored maintenance rates to 71.4–100.0% (Okumura, 23 Jun 2026). The paper interprets this as context-dependent suppression of expression rather than an underlying capability limitation, and proposes multi-agent architectures that separate proposal generation from causal auditing (Okumura, 23 Jun 2026).

Question-answering systems create an analogous problem for human users. In systems that occasionally provide unreasonable responses, showing a scatterplot increased the plausibility of unreasonable causal claims, and a warning that correlation does not imply causation reduced the tendency to associate correlation with causation in some contexts (Law et al., 2020). The central design risk is an illusion of causality: correlational evidence presented with causal phrasing can make weak claims look persuasive (Law et al., 2020).

A more basic warning concerns what LLMs are doing when they “answer causally.” The “Causal Parrots” argument is that LLMs may talk about causality, but they are not causal (Zečević et al., 2023). The paper introduces meta SCMs, in which the variables of one SCM encode causal facts about another SCM, and conjectures that when an LLM succeeds in doing causal inference, it may be reciting the causal knowledge embedded in the data rather than performing causal inference in the Pearlian sense (Zečević et al., 2023). This suggests that fluent causal language is not evidence of grounded causal understanding.

At the same time, Causal Caution can be built into machine-assisted discovery. The CauTion framework for LLM-augmented causal discovery uses an algorithm ensemble, consensus filtering, annotation-free trust calibration, trust-weighted voting, and cycle repair (Peng et al., 2 Jun 2026). Its central idea is to use an LLM only where the algorithms are uncertain and only when the estimated reliability of the LLM justifies arbitration (Peng et al., 2 Jun 2026). Here Causal Caution is not mere hesitation; it is a system design principle that allocates epistemic authority conditionally.

The broader implication is that Causal Caution has both inferential and governance dimensions. It concerns what can be justified from data and models, but also how analysts, interfaces, and AI systems should behave when justification is weak.