The Myth and Reality of 'World Models': Empirical Boundaries of AI's Action Predictive Power

The core of this experiment lies in testing the strong interpretation of a 'world model' — specifically, whether it can accurately predict interventional outcomes even when confronted with the challenges revealed by the P11 theorem of causal inference. The P11 theorem (RQ-DB3 Report, lines 660–719) states that there exist two types of systems that can be entirely observationally equivalent, yet their interventional outcomes for the same action (do(X)) are fundamentally different. This implies that merely excellent fitting of observational data does not guarantee a model's ability to correctly infer the effects of actions. Our goal is not to disprove this mathematical theorem, but rather to evaluate, at a concrete operational level (P11-op), whether a frozen model relying solely on observational information fails in the face of such observational equivalence.

In addition to the P11 theorem, the experiment also relates to Proposition P10 (RQ-DB3 Report, lines 600–656), which explores the separability of state prediction capability and interventional prediction capability. If a model can successfully predict the next observation (state information) but performs poorly in interventional prediction, it would trigger the counter-evidence condition of P10, namely that 'the representation does not constitute a world model usable for control.' Therefore, this study delves into what aspects its so-called 'world model' encompasses, and whether these capabilities are independent or interdependent, by distinguishing between the model's prediction of regular observations (state prediction) and its prediction of the consequences of active interventions (interventional prediction).

It is important to emphasize that this experiment is not designed to test whether large models form a world model during pre-training, as the experimental environment does not support model parameter updates; instead, it assesses whether a frozen model, under specific test distribution and contextual conditions, exhibits controllable action prediction capabilities. This means that even if the experimental results show that the model cannot reliably predict interventions solely based on observations in an observationally equivalent environment, this conclusion cannot be directly extrapolated to the pre-training phase. Rather, it is limited to evaluating whether, given specific prompts and input contexts, the model can effectively utilize its existing representations for causal inference.

To rigorously investigate the model's causal inference capabilities, we designed controlled environments generated by pure Python/NumPy scripts (verified: numpy 2.5.3 available), meticulously constructed to be 'observationally equivalent but interventionally different'. For instance, a classic binary structure based on the P11 theorem: two environments, one where U causes X which then causes Y, and another where U causes Y which then causes X. Both are observationally identical in their joint distributions (e.g., X=Y half the time), but their interventional outcomes for do(X=1) are vastly different. Through precise control of variable names, value labels, presentation order, number of records, and sampling seeds, we ensured that the empirical observational distributions of the twin environments were not significantly different (verified by two-sample chi-squared test and Total Variation Distance TV<0.05). We also introduced symmetric noise with P(flip)=0.1 to transform equivalence into approximate equivalence.

The experiment consists of five experimental arms (A0 to A3) to systematically evaluate the impact of different information types on model performance. Arm A0 provides only observational records, serving as the main contrast to test the S-strong hypothesis (i.e., 'with merely good observational fit, the model can reliably identify action effects in these environments'). Arm A0p provides a placebo segment of equal length but causally uninformative text, used to isolate potential confounding effects of text length or mechanistic tone. Arm A1 directly provides the true mechanistic description, Arm A2 allows the model to query results from a limited number of random experiments (k=20 samples), while Arm A3 allows the model to perform limited active exploration (4 steps). By comparing the performance across these arms, we aim to quantify the practical gain in causal inference from different levels of information.

To precisely measure model performance, we defined four key Dependent Variables (DVs). DV1 is the identification rate (p_A), which is the proportion of queries where the model provides a definite answer consistent with the true interventional distribution in unidentifiable environments (random baseline is 0.5). DV2 is the unidentifiability identification rate (u_A), used to evaluate the model's ability to explicitly respond 'cannot determine', penalized by correctness in identifiable environments if it always abstains. DV3 is the state prediction accuracy (s_A), measuring the accuracy of predicting the next observation given history. DV4 assesses the model's confidence calibration ability through the Brier score and ECE (if logprob is unavailable, it will downgrade to using linguistic confidence binning), ensuring the model not only gives an answer but also understands its own uncertainty.

This experiment adopts a rigorous preregistered statistical framework, explicitly defining the null hypothesis H0 and alternative hypothesis H1. The null hypothesis H0 (S-strong holds, P11-op is inapplicable) posits that the model's identification rate p_A0 in the observation-only condition (Arm A0) reaches above 0.80, and the gain from additional information (Arms A1, A2, A3) is less than 0.15. The alternative hypothesis H1 (S-strong is disproven, P11-op is supported) requires p_A0 to be below 0.65, and at least one information arm to provide a significant gain of 0.15 or more (with the 95% confidence interval excluding 0 after Holm correction). These thresholds, including the Minimum Detectable Effect MDE=0.15 and the equivalence bound δ=0.10, are design values frozen before the experiment begins, ensuring objectivity and transparency in decision-making.

To ensure the robustness of statistical results, we will use environment-level cluster bootstrap (B=10,000 resamples) to calculate the 95% confidence intervals for paired differences (p_A-p_A0). Absolute identification rates will use Wilson 95% confidence intervals, corrected for design effects due to clustering. For multiple comparisons, the Holm-Bonferroni method will be applied to control the Family-Wise Error Rate (FWER) at 0.05 for the three main comparisons (A1-A0, A2-A0, A3-A0), while secondary endpoints like calibration and state prediction will use the Benjamini-Hochberg method to control the False Discovery Rate (FDR) at 0.10. The sample size design accounts for clustering effects (DEFF=2.5), ensuring that 120 unidentifiable environments (20 abstract structural families × 6 parameter/surface variants) have at least 80% statistical power for an MDE=0.15 under conservative assumptions.

The final experimental results will be concluded based on a predefined three-state decision table: support, reject, or inconclusive. Before drawing any directional conclusions, a strict leakage audit must be passed, for example, the difference between the placebo arm A0p and A0 must be within the equivalence bound, and blind adjudicators must not be able to distinguish twin environments solely from observational records. If the audit fails, regardless of point estimates, the result will be deemed 'inconclusive'. Notably, 'rejecting' the S-strong hypothesis (i.e., that the model can identify action effects solely from observation) requires a higher evidence threshold, including replication of effects across different environment families and a second model (e.g., DeepSeek), to prevent misinterpreting potential leakage as groundbreaking model capability. This strict decision process aims to ensure the reliability and credibility of the experimental conclusions.

The core analysis of this study will be based on the main dataset D2, a collection of 185 synthetically controlled environments automatically created by generation scripts. This includes 120 unidentifiable environments that are observationally equivalent but interventionally different, 30 identifiable control environments (for validating DV2), 20 randomly labeled negative controls (for calibrating significance), and 15 environments for development and calibration. The D2 generation process includes seeds, equivalence test reports, and encrypted label tables, ensuring experimental reproducibility and impartiality. Importantly, D2 is the only dataset used for testing the main hypotheses, and its design aims to maximize the isolation of causal inference complexity, excluding noise and bias from real-world data.

In addition to D2, the study includes 41 Arabic business frozen queries (D1, verified path: `/research-opc-20260915/research/arabic-evaluation/ar_biz_eval_v1.jsonl`, etc.) as a secondary dataset, primarily for external validity and leakage probes. D1 tasks cover translation, intent recognition, Q&A, etc., and already possess automated scoring mechanisms. However, D1 itself does not contain causal intervention structures, thus it does not directly participate in the P11-related causal inference main hypothesis testing. Its role is to: verify whether conclusions from synthetic environments have surface ecological validity (e.g., if A0 performance under an 'Arabic business shell' is significantly better than a synthetic shell, it might alert to domain priors or data leakage). Furthermore, D1 serves as a baseline for model pre-training contamination, used for n-gram/embedding overlap and canary auditing.

To strictly control experimental contamination and ensure the purity of results, we have taken multiple measures: all test sets are allowed a one-time sealed access only; analysts remain blind to the true labels during the data collection phase; the main analysis script is frozen and hashed before data collection. Environment families are segmented by structural families, with 4 out of 20 families specifically reserved for cross-family extrapolation validation. Simultaneously, n-gram overlap and canary string detection will be performed to identify whether the model might have 'seen' text highly similar to the test set during pre-training. The discovery of any contamination signs will lead to the relevant results being downgraded to 'inconclusive' rather than allowing them to influence the final conclusions, thereby maintaining the scientific rigor of the experiment.

This experiment foresees several potential risks and has planned mitigation strategies. One of the biggest risks is 'environment leakage', where the model performs unusually well in Arm A0 (p_A0 ≥ 0.80), which might imply that the test environment design inadvertently leaked additional information. To mitigate this risk, we will first perform a strict auditing process (referencing Section 4.3), including testing the placebo arm A0p and the ability of blind adjudicators to distinguish. If the audit fails, the experiment will be redone, or the surface text will be rewritten into an Arabic business context for reverse verification. Ultimately, if the audit fails, the results will be deemed 'inconclusive' to prevent misinterpreting leakage as a true model capability.

Another key risk is 'positive control failure', where even with mechanisms, experiments, or exploratory information provided in Arms A1, A2, or A3, the model's performance remains similar to Arm A0 (identification rate close to 0.5). This may indicate that the task exceeds the capabilities of current models. In such cases, we will attempt to reduce the number of interfering dimensions, increase the experimental sample size, or provide more explicit mechanistic descriptions. If there is still no significant gain after improvements, the conclusion will be downgraded to 'inconclusive' rather than supporting any specific hypothesis. Furthermore, we are also concerned about the risk of 'degenerate solutions', such as the model consistently choosing 'cannot determine' to achieve a high u_A value; for this, DV2's certified score will penalize such indiscriminate abstention, ensuring the model 'dares to answer when it should, and abstains when uncertain'.

At the operational level, model access restrictions pose a non-negligible risk, particularly concerning the Codex CLI quota for gpt-6-astra. It has been verified that the local `settings.yaml` does not contain direct credentials for gpt-6-astra. If access cannot be obtained or is quota-limited, the alternative is to downgrade the conclusion to 'single model + dual time-point replication' and explicitly state the limitations on external validity in the report. If the API cannot return logprobs, calibration assessment will be downgraded to using linguistic confidence binning, but this will not affect the identification rate judgment as the primary DV. The most fundamental principle is: any failure at any stage will prioritize downgrading the conclusion to 'inconclusive', rather than relaxing the frozen thresholds (MDE=0.15, τ_strong=0.80, etc.), to ensure the scientific rigor and reliability of the study's conclusions.