Real Markets and Serious Pushback

Moving from simulation to reality runs into a hard empirical obstacle, and understanding it explains why there is so little field evidence.

Suppose prices in some market are high. To attribute that to algorithmic collusion you would need to know the competitive benchmark price, which is unobservable; which firms use pricing algorithms, which is usually not disclosed; when they adopted, which is rarely announced; and that nothing else changed at the same time.

High prices have many ordinary explanations: costs rose, demand strengthened, a competitor exited, the product improved. Distinguishing those from algorithmic effects requires variation you can exploit.

Worse, adoption is endogenous. Firms choosing pricing software are not a random subset. They may be larger, better managed, or facing different competitive conditions, any of which affects margins directly. Comparing adopters to non-adopters therefore measures selection as much as effect.

The German retail gasoline study is the field's landmark precisely because it solves these problems rather than assuming them away.

"Algorithmic Pricing and Competition: Empirical Evidence from the German Retail Gasoline Market" by Stephanie Assad, Robert Clark, Daniel Ershov, and Lei Xu appeared in the Journal of Political Economy, volume 132, number 3, pages 723 to 771, in 2024. It is the first empirical analysis of the relationship between algorithmic pricing and competition.

The setting is unusually favourable. German fuel retailers are required to report price changes, so researchers observe prices at high frequency across thousands of stations. Pricing software became widely available in 2017, giving a natural adoption window. And local markets are well defined, since stations compete with their geographic neighbours.

Two methodological moves make the results credible.

Adoption is not announced, so the authors identify adopting stations by testing for structural breaks in markers of algorithmic pricing, such as changes in the frequency and pattern of price updates. Most detected breaks cluster around the period when algorithmic pricing was introduced, which is the validation you want.

And because station-level adoption is endogenous, they instrument using brand headquarter-level adoption decisions, which shift a station's likelihood of adopting without being driven by that station's local conditions.

The headline numbers are these. Adoption increases margins by 9 percent, but only in non-monopoly markets. In duopoly markets, market-level margins do not change when only one of the two stations adopts, but increase by 28 percent in markets where both do.

Read the pattern rather than the numbers, because the pattern is what carries the argument.

If pricing algorithms simply made firms better at extracting value from their own demand curve, a monopolist would benefit most, having no competitor to worry about. Monopoly markets show no effect.

If the benefit came from responding faster than rivals, a single adopter in a duopoly would gain at its rival's expense. Single adoption changes nothing at the market level.

The gain appears only when competitors both adopt, which is precisely the condition under which two algorithms can interact. That is the signature of a competitive-interaction effect rather than an efficiency effect, and it is why this study is cited as the strongest field evidence that algorithmic pricing can affect competition.

It is worth being disciplined about the inference, because this result gets stretched.

The study measures margins, not strategies. It shows that when both stations in a duopoly adopt pricing software, market-level margins rise substantially. It does not observe the algorithms, their code, or their internal logic, and it cannot show a punishment-and-recovery structure of the kind Calvano identified in simulation.

Alternative explanations survive. Both firms responding faster to cost shocks could raise margins without any strategic interaction. Software might reduce pricing errors that previously left margin on the table. Adopting stations might change other practices at the same time.

The authors are measuring an outcome consistent with softened competition. That is meaningfully different from demonstrating the mechanism.

And the setting has features that may not generalise: a homogeneous product, mandatory price transparency, small numbers of local competitors, and frequent repeated interaction. Those conditions are close to ideal for tacit coordination of any kind, algorithmic or human.

Which brings us to the substantial body of work arguing the simulation results themselves are fragile.

The most direct challenge attacks the parameter settings.

Bichler and colleagues report that Abada and colleagues (2024) demonstrated that Q-learning with sufficiently large exploration parameters shows no collusion.

The logic is straightforward once stated. Collusion in these models rests on a stable pattern of mutual expectation: each agent's value estimates encode that high prices persist. An agent exploring frequently keeps deviating from the cooperative price at random, which disrupts the pattern before it can consolidate and teaches both agents that high-price states are not reliable.

So the collusive outcome depends on exploration being low enough to let the pattern stabilise. That is a parameter choice, not a property of Q-learning.

This is a serious objection because there is no principled way to say which exploration rate is realistic. Nobody knows what values deployed pricing systems use, if they use reinforcement learning at all. The simulation literature chose parameters that produce interesting dynamics, which is scientifically reasonable and also means the results are conditional on that choice in a way that headline summaries omit.

Two further lines of criticism attack different points.

Q-learning may not converge to collusion easily. Bichler and colleagues cite den Boer and colleagues (2022) as providing detailed analysis arguing that Q-learning would not lead to collusion easily. This is a theoretical challenge: the convergence properties that make the phenomenon appear robust in simulation may hold only under restrictive conditions.

Learned collusion may not survive a change of environment. Eschenbaum and colleagues (2022) found that collusion breaks down when trained offline policies are applied to different market environments.

The second objection is the more damaging for real-world relevance. A pricing algorithm deployed in an actual market faces shifting demand, entry and exit, cost shocks, promotions, and product changes. If a collusive policy learned in one environment collapses when the environment moves, then the simulation setting, a stationary market with fixed participants running for an enormous number of periods, may be doing the essential work.

Bichler and colleagues summarise the field's position directly: although experimental research has demonstrated that specific reinforcement learning algorithms can learn to maintain prices above competitive equilibrium levels in simulated environments, theoretical understanding of when and why such outcomes occur remains limited.

The dispute is not about whether the simulations ran correctly. Both sides agree on what the code did. The disagreement is entirely about how far those results travel: to other parameters, to moving environments, and to the software firms actually deploy.

The defensible position accommodates all the evidence rather than choosing a side.

Two gotchas for reading anything in this area. First, simulation results and field results are different kinds of evidence, and combining them into "algorithms collude" hides that the simulation shows a mechanism without a market and the field study shows a market outcome without a mechanism. Neither delivers both halves.

Second, the policy question does not wait for the science. Regulators must decide how to treat pricing software now, with the evidence in this state.

That gap between unsettled science and immediate legal necessity is where the final lesson goes.