simulation.

Urban road congestion concentrates at signalized intersections, and along urban arterials the coordination — or at least the consistency — of signal operation is one of the few levers that a road authority can actuate at low capital cost. Signal operation is therefore a classical instance of critical infrastructure control, in which locally rational decisions propagate through a spatially extended system and jointly determine network-wide performance [1]. Within the smart-cities research agenda, adaptive signal control occupies a privileged position because the underlying decision problem is well posed (minimize delay, queues, or emissions subject to safety constraints), yet its empirical solution on real networks remains difficult.

Conventional practice rests on two families of controllers. Fixed-time plans are computed offline from historical flow measurements using classical timing theory, most influentially the cycle-length and green-split formulae of Webster [2]. They require no detectors and no online computation, but they are blind to demand variation between plan updates. Actuated controllers, by contrast, extend or terminate green intervals in response to detector occupancy, which makes them responsive to short-term demand fluctuations without any explicit traffic model. Between these families lies a broad spectrum of adaptive schemes, and in recent years Reinforcement Learning (RL) has become the most actively explored candidate for populating that spectrum.

RL formulates signal control as a sequential decision problem in which an agent observes a state of the intersection, chooses an action such as extending or terminating the current green, and receives a reward such as the negative of the total queue length. Tabular Q-learning, introduced by Watkins and Dayan [3] and presented comprehensively by Sutton and Barto [4], is the simplest instance of this idea: it requires no traffic model, no forecasting module, and no neural network, which makes it attractive for constrained roadside hardware and for interpretability. Deep multi-agent extensions have since produced impressive in-simulation performance on both synthetic and real-world data.

A learned policy may encounter demand levels and directional compositions outside its training distribution. Such tests reveal behavior that in-distribution evaluation does not measure. The present study examines one simple tabular design, without establishing that all existing studies omit shifts or that the design is deployment-ready.

The reported experiment uses a point-queue corridor with six intersections, 7,200 one-second steps per episode, and a nominal saturation parameter 1,800 vehicles per hour per approach. Nine demand regimes cross levels and directional biases, with six used in training and three held out. Each controller is evaluated on twenty arrival realizations per regime. Conditional bootstrap and rank-test summaries quantify evaluation variability, but not variability across trained policies or simulator implementations.

The study combines fixed-time, actuated, and learned controls with an explicit held-out demand set. A reported conservation check finds zero vehicle-count discrepancy across 540 evaluation episodes, but conservation does not validate the discharge-capacity rule. The large delay under held-out arterial demand motivates inspecting state abstraction and policy timing; those diagnostics suggest hypotheses rather than isolate causes.

Webster timing relates an isolated-intersection cycle and splits to critical flow ratios under its approximate delay assumptions [2]. It is a standard engineering comparator, not universally optimal for a stochastic corridor with uncoordinated offsets. Directional demand changes and coordination can affect performance.

Point-queue models trade vehicle-level detail for speed. They differ from microscopic car-following simulation and from finite-storage cell-transmission models [5]. Queue integrals can summarize simulated waiting, but traffic-capacity fidelity depends on the discharge rules. Omitting spillback, turning, and platoon dynamics does not have a universally conservative effect.

Between fixed-time plans and learning-based controllers lies model-based adaptive control, of which constrained model predictive control is the most developed exemplar [6]. These methods optimize signal sequences over a rolling horizon from an explicit prediction model; their performance therefore depends on model quality, and their computational load scales with the prediction horizon and network size. Actuated control occupies the opposite, model-free corner: a gap-out rule terminates green when detectors report no waiting or arriving vehicles, subject to minimum and maximum green constraints. Actuated logic is local, cheap, and — as this study confirms — a demanding baseline for any learned controller.

RL-based signal control originates with tabular methods. Multi-agent deployments such as the system of El-Tantawy et al. [7] demonstrated intersection-level Q-learning agents that coordinate implicitly through the environment. The experimental review of Mannion et al. [8] surveyed RL algorithms for adaptive signal control and highlighted two recurrent weaknesses of the literature: heterogeneous simulation environments that impede comparison, and evaluation protocols dominated by in-distribution demand. The availability of large-scale traffic data and neural-network function approximation [9] subsequently enabled deep RL controllers such as IntelliLight [10], which learns expressive state-action mappings beyond the reach of lookup tables. Across this spectrum, tabular Q-learning retains two advantages that motivate revisiting it: its policy can be inspected cell by cell, and it can be executed on hardware with no floating-point accelerator.

The present gap is a scoped comparison of one learned tabular controller with two engineering references across an explicit demand split. It does not claim that asymmetric shift failure is absent from all prior work. The simulator and comparator information sets must be verified before conclusions are generalized.

The question is whether this tabular implementation retains low delay when demand shifts outside its training set. The network and nominal demand streams are held fixed across reported controller comparisons, while controller sensing and phase guards differ. Thus a measured difference reflects the complete designs, not only their decision rules.

RQ1 asks how the learned controller performs on training demand regimes; RQ2 asks how it transfers to excluded regimes relative to fixed-time and actuated control. H1 predicts lower delay than fixed time on training regimes, and H2 predicts that the advantage persists under the held-out shifts. These are designated comparison questions; a dated pre-evaluation protocol is not established. Rank-test summaries are conditional on the reported simulator, arrival realizations, and one trained policy.

Demand scenarios cross three demand levels — low (×0.65), base (×1.00), and high (×1.20) — with three directional biases: balanced (1.00, 1.00), EW-heavy (1.25, 0.80), and NS-heavy (0.80, 1.25), where the pairs are multipliers on (arterial, cross-street) base demands of 600 and 280 veh/h. The resulting nine regimes are split by a fixed protocol: Low / balanced, Low / EW-heavy, Base / balanced, Base / NS-heavy, High / balanced, High / NS-heavy are used for training, while Low / NS-heavy, Base / EW-heavy, High / EW-heavy are held out. The held-out set therefore contains one cross-street-heavy regime at low demand and the two arterial-heavy regimes at base and high demand, which lets us test generalization in both directional directions. All levels apply the same multipliers to both travel directions, so no level implies directional asymmetry by itself.

The described seed scheme uses base seed 42, training arrivals [42,2,k], evaluation batches [42,3,j], and bootstrap seeds [42,7000,n]. A common-random-number comparison requires exogenous arrival arrays to be identical across controllers, independently of their actions and other RNG calls. Twenty episodes per regime and 10,000 bootstrap resamples quantify conditional arrival variability. They do not estimate training-seed variability, because only one final learned policy is described. Holm adjustment covers 27 per-regime contrasts.

The source reports 168 s for training and 213 s for the complete pipeline. Reproduction requires actual code, environment, streams, learned Q-tables, and timing logs. Policies are frozen for evaluation. Matching arrival batches does not resolve the sensing, phase-guard, and service-capacity differences.

Table 4 retains the source conditional rank-test summaries. Q-learning reportedly has lower delay than fixed time in 146 of 180 paired episodes, yet higher pooled mean delay (36.7 versus 24.3), because severe failures outweigh smaller wins. Wilcoxon signed-rank direction and arithmetic mean direction are different summaries. Actuated control has lower reported delay across the paired comparisons. Pooled tests across heterogeneous regimes and reused policy parameters require an explicit target and dependence treatment; they do not establish field reliability or simulator correctness.

The source reports Holm-adjusted per-regime p-values and large rank-biserial effects. Bootstrap intervals with twenty episodes reflect arrival variability conditional on one learned policy. Narrow intervals cannot account for untested training seeds, simulator defects, changed sensing/action guards, or external traffic dynamics. Original vectors, test settings, and common arrival arrays are needed to verify the reported statistics.

The training-regime means support an advantage of the tested learned policy over the fixed-time plan within the reported simulation. The actuated implementation has lower displayed delays throughout. The comparison does not establish that reward design or decentralization alone caused the gain, because state abstraction, phase guards, sensing, and simulator interactions are bundled.

Held-out behavior is asymmetric in the reported results: low NS-heavy demand retains an advantage, while base/high EW-heavy demand loses it. The training curriculum covers high NS-heavy demand but only low EW-heavy demand. Sparse visitation and demand coverage are plausible contributors, not isolated causal findings from one trained policy.

Queue bins above thirteen alias moderate and large queues, so the state cannot distinguish their magnitude. The green-share summaries require a common denominator and do not demonstrate capacity below demand. The 60 s maximum green also does not make arterial-heavy allocation impossible: with EW green 60 s, NS minimum 10 s, and two 3 s amber periods, a feasible full-cycle EW fraction is 60/76≈78.9%, nominally 1,421 vehicles/hour. This does not prove an optimal or safe policy, but refutes an impossibility argument based on the action guards alone. Simulator service rules and phase traces must be examined before explaining the collapse.

Late-training spikes and weak variation in reported EW shares motivate further state and timing audits. They do not establish catastrophic forgetting in tabular Q-learning; the neural forgetting source [12] concerns a different model class. Controlled comparisons with finer bins, arrival features, curriculum variants, and multiple training seeds are needed.

Gap-out control responds directly to arrivals and queues, but its information and guard limits differ from the learned policy. Its strong results show the value of including an engineering baseline in this simulator. They do not imply universally demand-proportional green, a generalization guarantee, or a field default.

Evaluation should include excluded demand regimes, actuated references, and transparent timing diagnostics. Simulator conservation and service-capacity tests are separate requirements. The current capacity defects must be resolved and the comparisons rerun before using the displayed delays as physically validated outcomes. A practical learned controller would need an adequate state, feasible phase guards, representative demand coverage, and robust validation against comparable engineering controls. This synthetic experiment does not support a field deployment recommendation. Arrival features and finer queues are testable improvements, rather than established remedies.

The point-queue model omits turning, spillback, platoon dispersion, pedestrians, and coordination. The unbounded unused-credit rule and empty-green pass-through require correction/validation; their effect is not known to be 2.6% everywhere or equal across controllers. The uncoordinated fixed-time baseline is not the best possible corridor plan. One curriculum and one trained policy limit inference, while Poisson stationary demand omits incidents and within-episode transitions. No real traffic data validate transfer.

Reproducibility requires the simulator, controller implementations, immutable arrival batches, all per-episode metrics, Q-tables, statistical code, and software versions. The described environment uses Python 3.12.14, NumPy 2.1.3, SciPy 1.14.1, scikit-learn 1.5.2, and matplotlib 3.9.2 [11], [13–15]. A programmatic builder can reduce transcription errors but does not certify service capacity or inferential validity. The supplied manuscript does not establish an archived code/data release or bit-for-bit reproduction.

The reported six-intersection simulation shows lower learned-policy delay than fixed time on training regimes and a large failure under held-out high arterial demand. Actuated control has the lowest displayed mean delays. These are conditional observations of one policy in a point-queue implementation. Unbounded service credit, empty-green bypass, unequal sensing/phase guards, and timing-denominator ambiguity must be resolved before attributing the failure or claiming physically valid controller performance. Subsequent tests should rerun a capacity-validated simulator, match comparator information and actions, replicate training seeds, and retain held-out demand evaluation.

No external funding was received for this research.

All data are synthetic/simulated with documented generative models and fixed random seeds (Poisson arrival processes on a queue-based corridor simulator; no real-world data were collected or used). No human subjects, animals, or personal data were involved in this research.

The authors declare no competing interests.

The source manuscript reports that this manuscript and the associated code and analysis were produced with AI assistance under the Interdisciplinary Research Portfolio Program. Its claim that all numerical results originate from archived, seeded experiment code requires author confirmation and access to the versioned code and raw outputs; no accessible archive identifier is supplied here.

A public repository and archived version of the study-specific code and raw outputs are not specified.