The optimal execution problem arises when an institutional trader must purchase or sell a large quantity of shares before a deadline at minimal cost. Almgren and Chriss [1] derived the classical solution as a mean-variance optimization under linear market impact, producing deterministic execution schedules. Perold [10] introduced implementation shortfall as the standard cost metric. Time-Weighted Average Price (TWAP), splitting an order into equal tranches at equal intervals, serves as the practical regime-blind baseline. All these approaches assume stationary market conditions and cannot adapt to regime shifts that characterize real markets.

Amrouni et al. [2] introduced the CTMSTOU simulation environment, demonstrating that regime-aware hand-coded rules outperform regime-blind strategies. Paper I [6] showed that flat Proximal Policy Optimization (PPO) agents cannot replicate this advantage even with the true regime label in the state space, identifying the failure as structural. Paper II [7] validated that HMM uncertainty signals are empirically predictive of execution quality when aggregated over 3–10 days, establishing the temporal threshold that motivates this study.

Survival analysis models the time until an event, accommodating right-censored observations where the event has not yet occurred at the end of the observation window. The Cox proportional hazards model [3] estimates covariate effects on the hazard function semi-parametrically. The Weibull AFT model [4] assumes a parametric form for the survival time distribution, with the AFT parameterization expressing covariate effects as log-time multipliers directly interpretable as duration accelerants. The Weibull shape parameter ρ determines the hazard structure: ρ < 1 implies decreasing hazard (the longer a regime persists, the less likely it is to end), ρ = 1 implies constant hazard (memoryless), and ρ > 1 implies increasing hazard (regimes become more likely to end as they age).

Survival models have been applied extensively in biomedical research and engineering reliability [4] but have not, to our knowledge, been applied to regime duration prediction for execution. The application is natural: a bearish regime is an ongoing event with a start date, and the question of how much longer it will persist maps directly to the survival analysis framework.

Hamilton [8] established the theoretical foundation for Markov-switching models in financial time series. Recent execution systems assume HMM regime signals are informative without testing this empirically: TradeR [12] proposes a two-level hierarchical architecture motivated by regime diversity; EarnHFT [11] trains separate agents per market trend with an HMM-based router; Xu et al. [13] use a mixture-of-experts framework with regime states determining mixing weights. Lopez de Prado [9] provides a comprehensive treatment of overfitting risks in financial machine learning that motivates our out-of-sample validation design. Paper II [7] provides the empirical validation these architectures assume: signals are informative but only at multi-day aggregation horizons of 3–10 days.

We collect daily open-high-low-close-volume (OHLCV) data for eight assets via yfinance over a five-year period (2020-01-01 to 2024-12-31): three equity index ETFs (SPY, QQQ, IWM), two cryptocurrencies (BTC-USD, ETH-USD), one commodity ETF (GLD), one bond ETF (TLT), and one large-cap equity (AAPL). Equity assets yield approximately 1,237 trading days; cryptocurrency assets yield 1,806 calendar days due to continuous trading.

These eight assets are identical to those studied in Papers I and II, a deliberate choice serving two purposes. First, a consistent asset universe enables direct cross-paper comparison: the survival model results here can be related to Paper II’s aggregation-window findings and Paper I’s RL failure analysis without confounding from different asset coverage. Second, the set was originally constructed to span the widest feasible range of asset-class heterogeneity relevant to institutional execution. SPY, QQQ, and IWM provide large-, mid-, and small-cap equity index exposure with structurally different regime dynamics; BTC-USD and ETH-USD represent cryptocurrency markets with distinct volatility scales and continuous trading; GLD captures a store-of-value commodity whose regimes are driven by risk-off flows rather than earnings cycles; TLT introduces interest-rate regime sensitivity absent from equity assets; and AAPL represents a large-cap single name where idiosyncratic events can dominate regime onset. This breadth ensures that the failure of survival-model-based adaptive windows is characterised across structurally heterogeneous regime environments rather than within a single asset class.

The five-year window is motivated by the survival analysis requirement: with a one-year window as in Paper II, the number of complete bearish regime instances per asset is too small (1–3) for any survival model to be fitted. With five years, we obtain 81 total bearish instances across all assets, providing sufficient pooled samples for class-level models.

We fit a 4-state Gaussian HMM using the identical procedure as Paper II: 40 random initialization seeds, Bayesian Information Criterion (BIC)-based covariance structure selection, and a minimum 3% state occupancy constraint. State labels are assigned via the same two-step scoring procedure (crash, bearish, transitional, bullish). The smoothing procedure suppressing single-day regime switches is retained. All HMM fitting is in-sample over the full five-year window; the out-of-sample contribution in this study comes from the temporal train/test split applied at the survival model level.

In Paper II, HMM fitting used a one-year window; extending to five years here is necessary to accumulate sufficient bearish regime instances for survival model estimation. We note that in-sample fitting over the full five-year window means that regime assignments in the test period (2023–2024) reflect information from the full sample; reported survival model results should therefore be treated as upper bounds on prospective predictive power.

Regime collapse. We collapse the four-state HMM sequence to a binary label: crash (state 0) and bearish (state 1) are merged into bearish; transitional (state 2) and bullish (state 3) are merged into non-bearish. This collapse is motivated by Paper II’s finding that the execution edge is concentrated in states 0–2. We acknowledge that crash and bearish states are structurally distinct and that pooling them may introduce heterogeneity; this is noted as a limitation in Section .

Instance extraction. A regime instance is a maximal contiguous run of the collapsed label. Each bearish instance is characterized by its start date, end date, duration in days, and covariates measured at regime start (Section ). Two censoring rules are applied. First, any instance still active at the last sample day is right-censored (event indicator = 0). Second, instances exceeding 120 days are treated as censored at that threshold, primarily affecting BTC-USD where a single regime lasted over two years.1

The 120-day threshold constitutes administrative censoring applied retrospectively; Section 5.3 confirms the decreasing-hazard finding is robust across alternative thresholds of 90 and 150 days.

Train/test split. Instances with start dates on or before 2022-12-31 form the training set; instances starting on or after 2023-01-01 form the test set. This produces 54 bearish training instances and 27 bearish test instances. Table 1 summarizes these per asset. BTC-USD contributes no test instances because the 2021–2022 cryptocurrency market downturn produced a single large bearish regime consuming the entire BTC-USD training allocation.

We use two covariates, both measured on the first day of each bearish regime instance:

I. Entropy at start (H0): HMM posterior entropy on the first day of the regime instance. Lower entropy indicates a cleaner, more well-defined regime transition. The hypothesis is that clearer regime detection at onset predicts more persistent regimes.

II. Stay probability at start (SP0): The transition matrix diagonal element for the current state on the first day of the instance. Higher stay probability indicates the model considers the state inherently persistent.

We exclude volatility at start (75% missing values in preliminary runs) and prior regime duration (produced extreme coefficients −0.93 log-time units on the AAPL pool, a clear overfitting artifact). Restricting to two covariates is statistically conservative and appropriate given instance counts of 3–19 per asset class.

We fit a Weibull Accelerated Failure Time model using the lifelines library [5]. The AFT parameterization expresses the log-survival time as a linear function of covariates:

log Ti = µ + β⊤xi + σϵi, (1)

where Ti is the duration of instance i, xi is the covariate vector at regime start, β is the coefficient vector on the log-time scale, σ is the scale parameter, and ϵi follows a Gumbel distribution (yielding Weibull marginal durations). Positive βj indicates covariate j is associated with longer regime duration. Covariates are standardized via StandardScaler. A penalizer of 0.1 (L2 regularization) is applied to stabilize estimation on small samples.

Model hierarchy. A per-asset model is fitted when the asset contributes at least 8 training instances. Otherwise, instances are pooled within asset class. If the pooled class also has fewer than 8 instances, the asset receives a median-fallback predictor. This hierarchy applies to GLD and TLT, which fall back to medians.

The threshold of 8 instances is based on a minimum-observations-per-parameter heuristic: The Weibull AFT model estimates three free parameters (intercept µ, two covariate coefficients βH0 and βSP0 , and scale σ), giving a parameter-to-observation ratio of 1:2 at n = 8. Although L2 regularization (penalizer = 0.1) permits estimation below this ratio, the threshold provides a conservative lower bound consistent with standard survival analysis practice for small samples. To assess sensitivity, we re-ran the model hierarchy with alternative thresholds of 6 and 10 instances: at nmin = 6, no additional per-asset models become available because the only affected assets (GLD, n = 5; TLT, n = 4) still fall below the lower threshold; at nmin = 10, SPY (n = 10) transitions to the pooled equity-index model, yielding a C-index of 0.384 (unchanged from the pooled result in Table 2) and leaving the main conclusions unaffected. The 8-instance threshold is therefore not a critical decision boundary for the reported results.

Predictive evaluation. Concordance index (C-index) measures whether the model correctly ranks pairs of instances by predicted duration. C-index = 0.50 corresponds to chance; C-index > 0.70 is conventionally useful in survival analysis.

For each day t in the test period within a bearish regime instance, the predicted remaining duration is:

R ˆt = max 1, T ˆ0 − dt (2)

where T ˆ0 is the Weibull AFT median survival time predicted from covariates at the start of the current instance, and dt is the number of days elapsed since the instance start.2 The adaptive window is:

Wtadapt = clip ⌈R ˆt⌉, Wmin, Wmax (3)

with Wmin = 3 (the Paper II temporal threshold) and Wmax = 21 (one trading month). On non-bearish days, Wtadapt = 1.

Eq. (2) uses a first-order approximation; we verified for SPY and ETH-USD that the exact conditional median leaves floor and cap percentages within 3 percentage points of those reported, so boundary collapse persists under the exact formula.

The execution simulation is identical to Paper II, Section 3.6. TWAP uses the daily open price. Regime-aware execution uses the prior day’s inferred 4-state label: crash days use the open (halt strategy); bearish and transitional days use the midpoint of open and prior close (patient limit order approximation); bullish days use the open (aggressive, same as TWAP). The per-day cost difference is:

δt = RegimeCostt − TWAPCostt. (3)

Negative δt indicates regime-aware execution outperforms TWAP.

For the fixed-window baseline, we compute rolling mean cost differences over W ∈ {1, 3, 5, 10, 21} trading days and test Spearman rank correlation with entropy:

ρW = Spearman Ht, δ ¯t,W (4)

The primary comparison is between the adaptive window and the fixed W = 10 baseline. Significance is assessed at α = 0.05 for two-sided tests. We define an adaptive win as: (i) ρadapt < 0 (correctly signed) and (ii) ρadapt < ρW =10 − 0.01 (meaningfully more negative).

Table 2 reports C-index, Weibull shape, and model type for each asset. No asset achieves C-index ≥ 0.50. SPY’s per-asset model achieves C-index = 0.200, substantially below chance. Pooled equity index (SPY, QQQ, IWM combined, n = 18) achieves C-index = 0.384. Pooled crypto (BTC-USD, ETH-USD, n = 19) achieves C-index = 0.376. The ETH-USD per-asset model (n = 14, C-index = 0.390) is the strongest result and remains below chance.

† GLD has ntrain = 5 and TLT has ntrain = 4; both fall below the minimum threshold of 8 for Weibull estimation.

Weibull shape and decreasing hazard. All fitted models exhibit Weibull shape ρ < 1 (range 0.129–0.711), indicating decreasing hazard in every asset class. In the decreasing-hazard regime, the probability that a bearish episode ends on any given day decreases as the episode ages. The two most extreme shape values, AAPL at 0.129 and pooled crypto (BTC-USD) at 0.149, produce distributions nearly indistinguishable from a heavy-tailed Pareto distribution: hazard drops precipitously in the first few days and then becomes essentially flat. This explains why boundary collapse is most severe for these two assets (see Table 4).

Fig. 2 shows fitted Weibull survival curves alongside empirical Kaplan-Meier estimates for the test set.

Table 3 reports Weibull AFT coefficients on the standardized covariate scale, together with standard errors and Wald-test p-values.

SEs are from the Wald-based covariance matrix returned by lifelines WeibullAFTFitter; L2 penalizer (λ = 0.1) slightly shrinks coefficients toward zero. The large SEs for AAPL (n = 8) reflect the minimal training sample; results for this asset should be interpreted with particular caution.

The entropy coefficient reverses sign between AAPL (−0.212) and all equity index models (+0.342–+0.635). The stay probability coefficient is positive for crypto assets and negative for equity indices and AAPL. These cross-asset sign reversals indicate neither covariate has a universal monotone relationship with bearish regime duration.

Four of five models show wholly non-significant coefficients (p > 0.10 in all cases), consistent with the near-chance C-indices. SPY is the exception: both its entropy coefficient (SE = 0.208, p = 0.002) and stay probability coefficient (SE = 0.169, p = 0.003) are statistically significant, yet SPY’s C-index of 0.200 is the lowest of any fitted model, substantially below chance. This apparent contradiction reflects the distinction between in-sample association and out-of-sample ranking: the coefficients capture a relationship on the log-time scale that is statistically reliable within the n = 10 training instances, but the C-index measures whether predicted durations correctly rank pairs of instances, a harder task. A C-index of 0.200 indicates that SPY’s survival model inverts the true rank order on 80% of comparable pairs, meaning the direction of the fitted relationship is reversed relative to the actual ordering. With only 10 training instances and the model’s decreasing-hazard Weibull shape (ρ = 0.711), spurious in-sample significance combined with anti-predictive generalisation is consistent with overfitting; the significant p-values should not be interpreted as evidence of genuine covariate utility. AAPL’s wide SEs (> 0.74 for both covariates) confirm that the n = 8 model is informationally vacuous regardless of the

Fig. 4 and Table 4 summarize the adaptive window distribution on bearish days in the test period.

For six of eight assets, more than 60% of bearish days are assigned either the floor or the cap.

Structural guarantee of boundary collapse. For every asset in the dataset, the training-set mean bearish regime duration exceeds Wmax = 21 trading days. Because the Weibull AFT median prediction is anchored to the sample mean on the log-time scale, all per-instance predicted durations are clipped to the cap before any covariate adjustment is applied. This is a distributional property of bearish market regimes, not a consequence of poor model fit: any parametric survival model fitted on these data would exhibit the same boundary collapse.

Horizontal dashed lines mark Wmin = 3 and Wmax = 21. The strongly bimodal distributions confirm that survival model predictions collapse to boundary values.

Table 5 reports Spearman ρ between entropy and rolling cost difference across all windows for the test period (2023–2024).

‡TLT received the median-fallback predictor (ntrain = 4); its adaptive window is a constant, not a covariate-informed survival prediction.

§AAPL has 47% of its bearish days clipped to Wmax = 21; the apparent win is cap-driven, not a survival prediction. AAPL is also unstable under execution model perturbation (Section 5.2).

The adaptive window achieves no genuine wins over W = 10. Importantly, fixed windows continue to show meaningful signals: ETH-USD achieves ρ = −0.240∗ at W = 21; IWM achieves ρ = −0.160∗ at W = 21; AAPL achieves ρ = −0.119∗ at W = 5. The failure is specific to the adaptive calibration mechanism, not to the

The two nominal adaptive improvements (TLT, AAPL) are boundary artifacts.

We tested whether adaptive windows help most for instances whose duration deviates significantly from the asset-class mean by splitting test instances into SHORT (< 0.5× class mean, n = 19), MEDIUM (0.5–1.5×, n = 5), and LONG (> 1.5×, n = 3) subgroups. The adaptive method does not outperform W = 10 for SHORT instances (pooled adaptive ρ = +0.064 vs. ρW =10 = −0.122). The MEDIUM and LONG subgroups are too small for reliable inference. The subgroup analysis provides no evidence that the adaptive mechanism works for its intended use case.

We distinguish whether the survival model failure is a data quantity problem or a covariate adequacy problem by subsampling the training set without replacement: for each n ∈ {4, 6, 8, 10, 12, 15, 18, 22, 28, 35, 45}, we draw 50 subsamples, fit a Weibull AFT model, and evaluate C-index on the remaining 54 − n instances. We use C > 0.55 as the minimum useful threshold (a C-index of 0.55 would translate to predicted durations meaningfully different from boundary values for a non-trivial fraction of bearish days).

nOOS = held-out rows per run. At n = 45, only approximately 9 OOS rows remain; higher variance reflects reduced evaluation stability.

C-index does not improve monotonically with n; it fluctuates around 0.48 across the entire grid. Neither the minimum useful threshold of C > 0.55 nor the conventional threshold of C > 0.70 is achieved in ≥ 50% of runs at any sample size, ruling out the data quantity hypothesis.

We add Gaussian noise (std = 10% of empirical std) to the cost difference series and re-run all correlations. AAPL’s nominal adaptive win is among the unstable results, confirming its ∆ρ = −0.021 edge does not survive mild execution model misspecification. Neither nominal apparent win reflects robust survival model performance.

C-index = 0.50 is chance. All models use the same two covariates and L2 penalizer = 0.1. Cox C-indices are training-set statistics only.

The Cox proportional hazards model [3] imposes no parametric form on the baseline hazard, removing the decreasing-hazard shape constraint that forces Weibull predictions to collapse. On the training set, Cox achieves substantially higher C-indices (0.561–0.685). Whether this reflects genuine signal or training-set overfitting requires OOS verification with a larger regime instance pool, which we flag as the highest-priority open question.

Fitting univariate Weibull AFT models for each covariate individually yields all C-indices below chance (range 0.434–0.478). Prior regime duration, a naive strawman, achieves C = 0.529, marginally above chance but far below the useful threshold of 0.60. Fitting separate models for crash-origin (n = 35) and bearish-origin (n = 19) instances yields C-indices of 0.435 and 0.353 respectively, both lower than the pooled model (0.440). Adding five additional OHLCV features yields all-pooled C = 0.404, a decline of ∆ = −0.036 from the baseline; richer covariate sets do not improve duration prediction.

The sample size simulation is the most important result in this paper. The C-index curve is flat from n = 4 to n = 45, with no upward trend under Weibull AFT. A data quantity failure would show C-index increasing with n, eventually crossing the useful threshold. A covariate adequacy failure shows no upward trend regardless of n. Our results clearly indicate the latter for parametric models.

Entropy measures the HMM’s uncertainty about which of the four states the market is in on a given day. Stay probability measures the transition matrix diagonal. Neither signal captures why a particular regime episode will be shorter or longer than average. The factors that determine individual regime duration, the specific macroeconomic catalyst, the persistence of order flow imbalance, the sequencing of news events, are not encoded in the HMM posterior.

A critical distinction explains why these signals succeeded in Paper II but fail here. In Paper II, they predicted execution quality at the population level: aggregated over many days and regime instances, higher entropy correlated with worse execution. Individual regime duration, by contrast, is determined by the specific catalyst that ends each regime, an event orthogonal to the HMM posterior derived from daily price and volume.

All Weibull shape parameters are below 1.0, indicating decreasing hazard in every asset class. Economically, this reflects momentum in regime persistence: once a downtrend is established, it tends to continue because reduced investor confidence, deleveraging cycles, and feedback from declining prices to fundamentals reinforce themselves over time.

An alternative explanation deserves mention: unobserved heterogeneity (frailty). If bearish regimes come in two unobserved types, short shallow corrections and long structural downtrends, the pooled hazard will appear to decrease even if each subtype has constant hazard, because the short-duration type is progressively removed from the risk set. We note that frailty and intrinsic decreasing hazard produce identical implications for adaptive window design: in either case, the survival function is nearly flat and predictions collapse to boundaries.

The failure of adaptive calibration does not invalidate the Paper II finding that fixed temporal aggregation reveals genuine execution signals. Table 5 confirms this: ETH-USD achieves ρ = −0.240∗ at W = 21, IWM achieves ρ = −0.160∗ at W = 21, and AAPL achieves ρ = −0.119∗ at W = 5 in the 2023–2024 test period. The Paper II temporal threshold result replicates out-of-sample. The recommendation from Paper II stands: aggregate HMM uncertainty signals over 3–10 days before using them to filter execution strategy.

Two conditions would need to hold simultaneously. First, the survival model would need C-index > 0.60. The Cox PH result is the first indication this bar may be reachable, but requires OOS verification. For parametric models, the simulation shows no covariate set tested here approaches this threshold.

Second, for parametric models, the duration distribution would need to exhibit increasing or constant hazard (Weibull shape ≥ 1). Assets where bearish regimes are driven by episodic catalysts with known approximate resolution windows (earnings cycles, scheduled central bank meetings, index rebalancing dates) are structurally more likely to exhibit ρ ≥ 1. Future work targeting government bond futures around central bank meeting cycles, with macro-calendar covariates and OOS Cox evaluation, represents the most promising path.

Papers I–III form a complete characterization of the HMM regime-awareness framework in execution. Paper I [6] showed that PPO cannot learn regime-conditioned behavior even with the true regime label. Paper II [7] showed that HMM signals require multi-day aggregation (3–10 days) before they predict execution quality. This paper shows that the specific aggregation horizon cannot be adaptively calibrated from HMM-derived regime start covariates via parametric survival models.

Together, these results suggest the practical path to regime-aware execution requires: covariates that encode the causes of individual regime duration (not just the HMM’s assignment uncertainty), and an architecture that explicitly operates at weekly timescales. The first requires data beyond daily OHLCV; the second is the hierarchical approach proposed by TradeR [12] and EarnHFT [11], which Papers I–III now provide empirical motivation for.

The execution simulation uses a simplified fill model; real limit order execution depends on queue position, intraday price path, and adverse selection. All HMM fitting is in-sample over the five-year window; HMM regime assignments in the test period reflect the full five-year history, possibly overstating regime clarity relative to production. The sample-size simulation is bounded by 54 available training instances. Instance counts per asset class are small enough that pooled models aggregate heterogeneous regime dynamics.

The crash–bearish collapse merges two structurally distinct sub-regimes; however, Section 5.4 shows separate crash and bearish models produce lower C-indices than the pooled model, ruling out subtype heterogeneity as an explanation. The 120-day censoring threshold is confirmed robust via Section 5.3. BTC-USD contributes no test instances, so the pooled crypto model’s test-period evaluation rests entirely on ETH-USD. The Cox PH training-set result requires OOS verification before revising the covariate inadequacy conclusion.