Experiments

How to run experiments on AI agents and workflows

May 27, 2026

min read

A graphic of a bar chart with an arrow pointing upward.

Scoring each step of an agent workflow and calling it an experiment is like grading every sentence in a report without checking whether the report answered the question.

The scores can all look fine while the agent completely fails the job it was supposed to do. That's the core problem this article addresses: AI agent experiments require a fundamentally different approach than prompt A/B tests, because the unit of measurement isn't a response — it's the entire workflow, from first tool call to final outcome.

This guide is for engineers, PMs, and data teams who are building or evaluating multi-step AI agent systems and need a rigorous way to test them. If you already run A/B tests on prompts or product features, you have the right instincts — but the methodology needs to change when agents maintain state, chain tool calls, and make decisions that compound across steps. Here's what you'll learn:

Why agent experiments fail when you apply prompt A/B tests logic to multi-step workflows
How to define metrics that actually reflect workflow-level success — task-completion rate, error recovery rate, step efficiency, and failure point attribution
How to structure controlled experiments around tool use, model selection, and workflow architecture using feature flags and gradual rollouts
The hard measurement problems unique to agent systems — non-determinism, long observation windows, and attribution across steps — and how to work around them
How to build a continuous improvement loop so your experiments compound into institutional knowledge instead of disappearing after each ship decision

The article moves in that order: from why the problem is structurally different, to what to measure, to how to run the experiments, to what can still go wrong, to how to make the whole program stick over time.

Why AI agent experiments are fundamentally different from prompt A/B tests

If you already run prompt A/B tests, your instinct when evaluating an AI agent will be to apply the same methodology — score each step's output, aggregate the results, and declare a winner. That instinct is wrong, and acting on it will produce experiment results that are not just incomplete but actively misleading.

The reason isn't a matter of scale or complexity. It's a structural mismatch between what prompt A/B tests measure and what agents actually do.

What traditional prompt A/B tests actually measure

A prompt A/B test evaluates a single transformation: one input goes in, one output comes out, and you score that output. The system is effectively stateless from the experiment's perspective. Each interaction is independent. You can measure relevance, accuracy, tone, or task completion for that one response — and because nothing that happened before affects what you're measuring, isolated scoring is valid.

This methodology works precisely because single-response systems have a more predictable execution model. The agent receives a prompt, reasons through the steps, and produces an output. That's the entire surface area of the experiment. Prompt A/B tests are well-designed for exactly this architecture — and only this architecture.

Why agents break the assumptions that make prompt A/B tests valid

Agents don't produce a single output. They maintain state across steps, make tool calls whose results feed subsequent decisions, and operate across a decision chain where each output becomes the next input. The evaluation unit isn't a response — it's a trajectory.

Consider a multi-agent fraud detection workflow where one agent analyzes transaction patterns, a second reviews customer history, an aggregator synthesizes both findings, and a validator checks the final output before a decision is made. Each agent's output is the input context for the next. A prompt A/B test can tell you whether the transaction analysis agent produced a well-formed output.

It cannot tell you whether that output was the right input for the customer history agent, whether the aggregator handled conflicting signals correctly, or whether the validator caught a downstream error that originated two steps earlier.

The coordination layer between steps — the decisions about when to call a tool, what to do with a tool's output, how to handle ambiguity before passing context forward — is entirely invisible to step-level evaluation.

The cascade failure problem

This is where step-level scoring stops being merely incomplete and becomes actively misleading. In a multi-step agent workflow, an error at step 2 doesn't produce a bad step-2 output that you can catch and flag. It corrupts the context that steps 3, 4, and 5 operate on.

Each subsequent step may execute correctly given the corrupted context it received — and score well on a local evaluation — while the overall task fails completely.

You can run a step-level evaluation that shows every individual output passing quality thresholds while the agent fails the actual job it was supposed to do. The scores are technically accurate and strategically useless.

This isn't hypothetical. A Cornell University study found that single-agent GPT-4 systems achieved a 2.92% success rate on complex planning tasks, while coordinated multi-agent systems reached 42.68% on the same benchmark. That gap isn't a prompt quality problem.

It's a workflow architecture problem — and no amount of per-step output scoring would have identified it, because the failure mode lives in the coordination between steps, not within any individual step.

The evaluation unit must be the workflow

The practical implication is straightforward: AI agent experiments must be designed to measure task completion at the workflow level, not output quality at the step level. The success metric for an agent experiment is whether the agent completed the task correctly end-to-end — not whether each individual response looked good in isolation.

This reframes what "winning" means. A variant that produces slightly lower-quality intermediate outputs but recovers from errors more reliably and completes more tasks is a better agent than one that scores higher on per-step evals but fails more often at the finish line.

GrowthBook frames this directly: when it comes to AI, "evals are just the tip of the iceberg — A/B testing is where real value gets created." Output-level evaluation is a starting point, not a measurement strategy. Connecting AI behavior to user outcomes requires measuring the workflow, not the response.

The four metrics that expose what step-level scoring misses in agent workflows

Knowing that workflow-level measurement is necessary is not the same as knowing what to measure. According to Galileo's State of Eval Engineering Report, 72% of AI teams believe comprehensive testing drives reliability — but only 15% achieve elite evaluation coverage.

That 57-point gap isn't a motivation problem. It's a measurement problem: teams are testing, but they're testing at the wrong granularity, disconnected from the business outcomes that actually matter. Four metrics close that gap.

Task-completion rate: the primary signal

Task-completion rate sounds obvious until you try to define it precisely. The metric isn't whether each step produced a plausible output — it's whether the agent actually accomplished the stated goal of the full workflow. That distinction matters because of what Confident AI calls "false task completion": the transcript says "done," the final output looks clean, but nothing in the real system actually changed.

This failure mode is completely invisible to output-only scoring. You only catch it by measuring at the workflow level, against ground truth.

Task-completion rate is your leading indicator for user satisfaction and retention. When it degrades, users notice before your dashboards do — which means instrumenting it properly is a prerequisite for everything else.

Error recovery rate: measuring resilience under failure

No agent workflow runs cleanly every time. The question isn't whether errors occur — it's whether the agent recovers from them without human intervention or a full abort. Error recovery rate measures exactly that: the proportion of workflow runs where the agent encountered a failure state (wrong tool call, bad argument, unexpected output) and successfully self-corrected.

The failure modes this metric is designed to catch include what practitioners call the "interrogation loop" — retry cycles that never converge, burning latency and compute while producing nothing. Low error recovery rate is a direct driver of elevated cost and degraded response time, which makes it a business metric as much as a quality metric.

Step efficiency: the cost hidden in the decision path

Every unnecessary tool call, redundant reasoning step, or circular summary has a price. Step efficiency — the number of steps required to complete a task relative to a minimum viable path — is a direct proxy for inference cost and latency. Confident AI's "budget burner" pattern describes this precisely: traces that look fine on the surface but are filled with reasoning thrash and circular summaries that advance nothing.

The qualitative complement to raw step count is turn relevancy — whether intermediate steps are actually moving toward the goal. Both require trace data to measure, but they answer different questions: step count tells you how much work the agent did, turn relevancy tells you whether that work was purposeful.

Failure point attribution: finding where workflows actually break

The step where a workflow degrades is often not the step where the failure becomes visible. A bad tool argument in step 2 might not surface as a wrong answer until step 6. This is why full LLM tracing isn't optional — it's the foundational instrumentation requirement. Without a complete trace of the decision path, failure point attribution is guesswork.

Galileo's finding that traditional metrics "don't capture agentic workflows where success depends on multi-step reasoning" points directly at this gap. Trace-level data is what converts a vague sense that "the agent is underperforming" into a specific, actionable diagnosis: this tool selection, at this step, under these input conditions, is where the workflow breaks.

Mapping workflow metrics to business outcomes

Each of these metrics connects to a concrete business dimension. Task-completion rate maps to user satisfaction and retention. Latency and support cost are where error recovery rate lands — every unrecovered failure is either a slow response or a human escalation. Inference cost and response time move with step efficiency. For failure point attribution, the downstream dimension is engineering velocity: faster diagnosis means faster iteration cycles.

Experimentation platforms that support custom SQL metrics and configurable metric windows let teams define these workflow-level outcomes as first-class metrics computed from their own data, rather than relying on proxy signals that don't reflect what the agent actually did.

GrowthBook's warehouse-native experimentation connects directly to your existing data infrastructure, so workflow-level metrics like task-completion rate and error recovery rate can be defined in SQL against your own event data rather than requiring a separate instrumentation layer. Metric correlation analysis is particularly useful here for detecting trade-offs: when you optimize for step efficiency, does task-completion rate hold? That tension is exactly the kind of question controlled AI agent experiments are designed to answer.

Structuring AI agent experiments around tool use, error recovery, and task completion

The core discipline of controlled experimentation — change one thing, hold everything else constant — sounds simple until you're staring at an agent system with a dozen moving parts. Which model is handling which subtask? Which tools are available at which step? How is the workflow decomposed? How aggressive are the guardrails?

Each of these is a variable, and without a deliberate isolation strategy, you cannot know which one caused the change in task-completion rate you observed. The operational challenge isn't conceptual — it's that most teams haven't formally defined their agent configurations in a way that makes controlled comparison possible.

Isolating the experimental variable in a multi-component agent system

Before you can isolate a variable, you have to name it precisely. Agent systems have four primary variable categories worth treating as distinct experimental dimensions: the prompt or instruction set, the model selection, the tool configuration (which tools are available, in what order, with what permissions), and the workflow decomposition (how subtasks are structured and delegated across steps or sub-agents).

The reason informal experimentation fails here is captured well by recent work on structured agent experiment design: "experimental conditions for agentic workflows are still largely specified in prose, making them difficult to compare, reuse, or audit". When your baseline and variant are described in natural language rather than formally encoded, you can't reliably determine what actually changed between them — and you certainly can't reproduce the experiment later.

The discipline of naming the variable precisely, encoding it consistently, and holding the other three categories fixed is what separates a valid agent experiment from an anecdote.

Feature flags as the mechanism for switching agent configurations without a deploy

The practical mechanism for switching between agent configurations in production — without a full code deploy — is feature flags linked directly to experiment assignments. Feature flags control which agent configuration a session receives (model version A vs. B, tool set with web search vs. without, prompt variant for the planning step), and the experiment tracks workflow-level outcomes against that assignment. GrowthBook supports attribute-based targeting rules so flags can be scoped to specific workflow contexts, task types, or user segments without affecting the full user base.

Gradual rollout is the right risk posture for AI agent experiments. Exposing 5% of traffic to a new tool configuration while monitoring error recovery rate as a guardrail metric gives you real signal without committing the full user base to an untested configuration.

If the new configuration causes error cascades — a real risk when a tool call failure at step 2 corrupts the rest of the workflow — an instant kill switch lets you deactivate it without waiting for a deployment cycle. Kill switches work instantly because flag evaluation happens locally: flip the toggle in the dashboard, the new rules propagate via the streaming connection, and every SDK evaluates the updated rule on its next check. No deploy required. That kill-switch capability isn't a convenience; it's a safety requirement for agent experiments where failures compound across steps.

A well-structured experiment schema supports this pattern directly: linked feature flags connect flag state to experiment assignment, guardrail metrics are a distinct category separate from primary goals, and experiment targeting rules enable conditional enrollment so you can scope an experiment to a specific task type — order processing workflows, say, rather than all agent sessions indiscriminately.

Treating architectural decisions as testable hypotheses

The most common mistake in agent experimentation is treating workflow decomposition and guardrail placement as fixed infrastructure rather than experimental variables. They aren't. Whether a task is handled by a single agent with a long prompt or decomposed into three specialized sub-agents with handoff logic is an architectural choice with measurable effects on task-completion rate and error recovery behavior. It should be tested, not assumed.

The practical implication: before running a prompt A/B test, verify that your current workflow decomposition isn't confounding the results. A suboptimal architecture will suppress the signal from any downstream prompt experiment — you'll be optimizing the instructions for a structure that itself needs to change.

Running controlled rollouts at the workflow level

The unit of randomization and measurement in an agent experiment is the workflow run, not the individual tool call or response. This matters for how you structure traffic splitting and how long you need to run the experiment. Agent workflows are typically lower-volume than web page views, which means reaching statistical significance takes longer.

Standard A/B testing requires you to decide your sample size upfront and wait until you hit it — which can mean weeks of waiting for low-volume agent workflows. Sequential testing is an alternative approach: you monitor results as they come in and stop the experiment when the evidence is strong enough to make a decision, without waiting for a fixed endpoint.

This avoids two failure modes: stopping too early because the first results looked promising, and running far longer than necessary because you committed to a sample size that assumed higher traffic than you actually have. For AI agent experiments specifically, where completed workflow runs are scarce, sequential testing is worth understanding before you set up your first experiment.

Targeting also matters more in agent experiments than in standard product experiments. The same configuration may perform very differently across task categories. Scoping enrollment to a specific workflow context — using prerequisite conditions on experiment phases — keeps your results interpretable and prevents a strong effect in one task type from being diluted by noise from another.

The hard problems in AI agent experiments: non-determinism, long horizons, and attribution

Well-designed agent experiments can still produce untrustworthy results. Not because the experiment was set up incorrectly, but because the measurement itself is structurally compromised. Engineers who already run A/B tests will apply familiar statistical intuitions to agent experiments — and those intuitions will mislead them.

The noise floor is higher, the observation window is longer, and the causal chain between a decision point and a final outcome is obscured by every compounding step in between. These aren't immature problems that better tooling will eventually solve. They're structural properties of how agents work.

The non-determinism problem — why agent experiments have a higher noise floor

A single LLM call produces different outputs even for identical inputs — that's just how language models work. An agent making ten tool calls compounds that randomness ten times over: the output of step one affects what step two receives, which affects step three, and so on. By the end of a ten-step workflow, two runs that started with the same input can have followed completely different paths.

As Arize AI puts it directly: "LLMs are non-deterministic — agents can follow strange paths and still arrive at the right answer, making debugging difficult." In a single-response evaluation, you can run enough samples to average out that variance. In an agent workflow, the same input can produce divergent execution paths entirely — meaning two runs of the "same" experiment may not actually be testing the same behavior at all.

This inflates outcome variance in ways that require larger sample sizes or longer run times to compensate for. But there's a subtler problem too. Anthropic has documented cases where agents succeed via unexpected paths that the grading logic doesn't recognize as success — producing false negatives.

When Anthropic tested Opus 4.5 on a flight booking task, the model solved the problem by discovering a policy loophole rather than following the expected resolution path. The agent succeeded; the evaluator marked it as a failure. If your grading logic can be outpaced by model behavior, your experiment results are measuring evaluator limitations as much as agent capability.

Long-horizon observation windows — how task duration distorts experiment timing

Standard experimentation practice says to run until you reach statistical significance. For agent workflows that take hours or days to complete, that heuristic breaks down. You cannot measure a partial workflow — an incomplete task looks identical to a failed one until it finishes.

Checking results before tasks complete produces misleading signals, and the peeking problem that affects all experiments is especially acute here because task completion times are variable and long.

This creates a direct tension with fast iteration cycles. If your agent handles multi-day workflows, a single experiment round-trip might take weeks before you have enough completed tasks to draw conclusions. Anthropic notes that "agents use tools across many turns, modifying state in the environment and adapting as they go — which means mistakes can propagate and compound." That compounding happens over time, which means your observation window must be long enough to capture the full propagation, not just the first few steps where things look fine.

Attribution across multi-step workflows — which decision caused the outcome?

When an agent fails at step eight, which of the preceding decisions caused it? The final outcome metric tells you that something went wrong. It doesn't tell you where. Databricks frames this precisely: "An answer may be correct, but the tool calls leading to it may be inefficient, risky or inconsistent. Evaluating only the final output can hide underlying reasoning failures."

This means teams need step-level instrumentation — tracing tool calls, intermediate state, and decision points — not just outcome logging. Without it, experiment results tell you that a configuration change moved a metric, but not why, which makes intelligent iteration nearly impossible.

Arize AI's framing is useful here: "Effective agent evaluation requires looking beyond final outputs to assess what the agent knows, what actions it takes, and how it plans." That's not a nice-to-have. It's a prerequisite for attribution.

The right tooling can help here: experimentation platforms that pull metrics directly from your data warehouse — rather than requiring a separate event-tracking layer — let you join trace data from your agent runs to the business outcomes you actually care about, like whether the user completed their task or came back the next day. But the tooling only works if the traces exist. If you're not logging tool calls, intermediate state, and decision points during every workflow run, no amount of downstream analytics infrastructure will give you attribution.

Replay-based testing environments — controlling for non-determinism

The most practical mitigation for both non-determinism and attribution challenges is replay-based testing: capturing real execution traces from production, then replaying them against a modified agent configuration in a controlled environment. Because the environment state, tool responses, and input sequence are held constant, you're doing an apples-to-apples comparison where only the agent configuration changes.

Anthropic's multi-turn eval harness design follows this pattern — a controlled environment, an agent loop, and a grading mechanism that evaluates the full execution, not just the final output.

Replay environments get closer to realistic testing standards than static benchmarks. But they come with a real cost: significant instrumentation investment upfront, and a structural limitation that replay environments may not surface novel failure modes that only emerge in live conditions with real users and real tool states. There's no clean solution here — only a more honest accounting of what your experiment results can and cannot tell you.

Building a continuous improvement loop for AI agent workflows

One-off experiments on agent systems tend to produce one-off insights. A team tests a new prompt, ships the winner, and moves on — only to revisit the same question six months later when a different engineer joins and asks why the workflow is structured the way it is. The institutional knowledge from that first experiment is gone.

This is the compounding knowledge problem that makes agent experimentation programs fail not at the experiment level, but at the program level.

The argument here isn't that individual experiments are useless. It's that their value multiplies only when they're treated as documented artifacts in a cumulative learning system rather than isolated tests that produce a binary ship/don't-ship decision. As GrowthBook's experimentation infrastructure puts it: "Each experiment may not have a large effect on your metrics, but many experiments might." That framing captures exactly what a continuous improvement loop is designed to exploit.

Establishing a baseline and iteration cadence

Before you can iterate meaningfully, you need a stable reference point. For agent workflows, that means documenting a control state with known task-completion rates, error recovery rates, step counts, and failure point distributions — the metrics covered earlier in this article. Without a documented baseline, you can't distinguish a genuine improvement from natural variance in agent behavior.

The iteration cadence question is trickier. There's no universal answer for how frequently agent teams should run new experiments, and any specific schedule would be arbitrary. What matters more is calibration: are you running enough bold experiments to generate real learning, or are you defaulting to safe prompt tweaks that win easily but teach you little?

Monitoring win rates and experiment frequency over time gives you a signal on this — a consistently high win rate often means the experiments are too conservative, not that the team is unusually skilled.

The practical loop is straightforward: establish baseline → run experiment → document result → update baseline → repeat. Each cycle should produce a reusable artifact, not just a deployed change.

Documenting experiments as learning artifacts

The documentation problem is worse for agent systems than for standard product experiments because the experimental variable could be a prompt, a tool configuration, a guardrail threshold, a workflow decomposition decision, or a model swap — and these are easy to lose track of across a fast-moving codebase. "Experimentation programs generate a lot of artifacts that can be hard to capture," as GrowthBook notes in describing the institutional knowledge problem directly.

What a useful learning artifact contains: the hypothesis going in, exactly what was changed, which workflow-level metrics moved and by how much, the conclusion, and the reason the experiment was stopped. These aren't just documentation hygiene — they're the inputs that prevent future teams from re-running experiments you've already run.

Some experimentation platforms use vector embeddings across experiment descriptions and hypotheses to flag potentially redundant experiments before they're launched, which addresses this problem at the infrastructure level rather than relying on team members to remember what was tested.

Character.AI's use of GrowthBook for iterative model comparison illustrates what this looks like in practice. Landon Smith, Head of Post-Training, described it this way: "We can compare different modeling techniques from the perspective of our users — guiding our research in the direction that best serves our product." That's the iteration loop operating as intended: each comparison informs the next research direction rather than producing a one-time answer.

Tracking cumulative workflow-level impact

Individual agent experiments frequently show small or ambiguous effects. A 2% improvement in task-completion rate might not clear statistical significance on its own, but ten such experiments compounding over a quarter represent a meaningful capability shift. The only way to see that is with a cumulative view across the full experimentation program — not just the most recent test.

This is where tooling like GrowthBook's Cumulative Impact dashboard becomes relevant: it aggregates the effect of all experiments on any given metric, making the program-level story visible to both the teams running experiments and the stakeholders who need to understand why the investment is worthwhile. Connecting that view to North Star metrics — task-completion rate, cost per workflow run, user satisfaction — closes the loop between individual experiment decisions and long-term business outcomes.

The observation that holds true across the AI agent community is that "there is no secret sauce" in the basic loop structure. The competitive advantage comes from how systematically you refine it. If the architecture is commoditized, the teams that win are the ones that accumulate the most rigorous institutional knowledge about what actually moves their specific workflow metrics — and that only happens through a program, not a series of one-off tests.

Three starting points for teams that have never run a controlled agent experiment

The through-line of this article is simple: AI agent experiments fail when you treat a workflow as a collection of responses instead of a single unit of behavior. Every section builds on that premise — from why cascade failures are invisible to step-level scoring, to why task-completion rate is the metric that actually connects to user outcomes, to why your workflow decomposition might be confounding every prompt experiment you've ever run.

Where you start depends on where you are. The right first move isn't the same for every team.

If you're not yet measuring task-completion rate at the workflow level against ground truth: That's your starting point — not a new experiment, not a new tool, just a measurement change. Define what "task complete" means for your specific workflow, instrument it against real outcomes rather than transcript output, and run your existing configuration against that baseline before changing anything else.

If you have workflow-level metrics but no trace instrumentation: Add tracing before your next experiment. Without a complete record of tool calls, intermediate state, and decision points, you'll know that a configuration change moved a metric but not why. That's not enough to inform the next experiment — you'll be iterating blind.

If you have both metrics and tracing: Identify the one architectural variable you've been treating as fixed infrastructure — your workflow decomposition, your guardrail thresholds, your tool selection logic — and design a controlled test around it. That's the experiment most teams should have run six months ago and haven't because it felt like "infrastructure" rather than experimentation.

GrowthBook's feature flag and experiment infrastructure is designed to support this pattern at each stage: gradual rollouts with guardrail metrics, linked feature flags for configuration control, and cumulative impact tracking so individual small wins add up to a visible program-level story.

The honest constraint to keep in mind: observation windows for agent experiments are longer than you're used to, and instrumentation takes real time to build. You will feel pressure to move faster than the data supports. A premature conclusion from an incomplete workflow observation is worse than no conclusion — it sends your team in the wrong direction with false confidence.

This article is meant to give you a clear, honest foundation for that work — not to make it sound easier than it is.

Related insights

Sign up for free

Take Growthbook for a spin, no credit card required.

Create my account

Example H2

See All Articles

Experiments

Feature Flags

CLI vs MCP: TLDR, it doesn’t matter as much as you think

Oct 21, 2026

min read

Your agent should know how to do the job whichever interface it uses.

Your coding agent can already run terminal commands. Your product manager's assistant can connect to remote tools. Both need to inspect the same experiment, understand the same metric, and prepare changes to the same feature flag.

That creates a familiar question: should you give them a CLI or an MCP server?

The usual answers mix several concerns. A CLI is easy to compose with scripts. MCP gives compatible clients a standard way to discover and invoke tools. Skills can supply the instructions that make either route useful. None of those statements tells you whether the agent knows your release process or can distinguish a draft from a live change.

For GrowthBook, the choice has become smaller. We've built the agent layer around a REST API and reusable workflow skills, then made those available through different interfaces. Your choice of CLI or MCP no longer needs to determine which product workflow your agent can understand.

It still determines how the agent connects, executes requests, and handles credentials. This article explains that distinction, shows the same disabled-flag operation through both routes, and gives you a way to evaluate the integration you actually intend to use.

The debate combines three different questions

Start with a specific job: prepare a release control for a new checkout flow. The agent needs to know which project owns checkout, which environments exist, what the default behavior should be, and whether the proposed flag key already exists.

Choosing an interface answers only part of that job.

How can the agent reach the product?

A command-line interface lets an agent invoke a program in an environment where it has shell access. That program can make authenticated API requests and return data. You can also run the same commands yourself, put them in scripts, and preserve output for inspection.

The Model Context Protocol architecture connects a host application to servers through clients. An MCP server exposes capabilities that a compatible host can discover and call. The host might be a coding environment, a desktop assistant, or another agent application.

These categories overlap. A terminal-based agent can also be an MCP client. A local MCP server can be a process launched by that client. A remote MCP connection can work without the host giving the model a general-purpose shell.

So “terminal agent” doesn't automatically mean “use the CLI,” and “MCP” doesn't automatically mean “remote service.” Ask what access the runtime provides before choosing the adapter.

What procedure should the agent follow?

An API can expose a create operation without teaching an agent when to use it. A syntactically valid feature flag might still have the wrong project, an ambiguous key, or a default value that doesn't match the application.

That's the job of a skill: reusable instructions for a recognizable task. The Agent Skills format gives those instructions a portable structure, including a skill entry point and supporting references. A workflow can describe the context to inspect, the sequence to follow, and the evidence to return.

For the checkout example, useful guidance says to resolve environments, check the permanent key, choose a value type, and create the flag disabled. Merely exposing a create command leaves those decisions to the agent's general knowledge.

Skills are also useful when the right answer is to take no action yet. “Create a flag” and “design an experiment” are related requests, but they can require different objects and sequencing. An agent needs enough product guidance to make that distinction.

What context makes the procedure relevant?

Even a good playbook needs the current product state. The agent should inspect the objects in your GrowthBook organization and, when it is changing application code, the repository's SDK initialization and tests.

Those are different sources of context. GrowthBook supplies flags, experiments, metric definitions, and other authorized product resources. Your coding runtime supplies the application files it can access. An MCP connection doesn't by itself grant repository access, and a CLI doesn't by itself explain your metric definitions.

Evaluate the combination: access to the product, a maintained procedure, and enough context to apply that procedure. A comparison that changes all three at once cannot isolate the effect of CLI versus MCP.

GrowthBook puts the durable parts below the interface

We separated the agent layer into responsibilities that can be reused. The product API exposes operations. Skills explain workflows. The interface connects the agent to those two layers.

This is the architectural shift behind GrowthBook's agent experience. Instead of making every client integration carry its own interpretation of experimentation, we can share the interpretation and change how it is delivered.

The API provides the operations

GrowthBook's REST API makes product objects addressable. An agent can inspect a project, retrieve a flag, or perform an authorized operation against those objects.

The rebuilt API described in GrowthBook 4.4 uses shared schemas to support types, validation, and API documentation. The CLI is generated from the API definition. That reduces the amount of separately maintained command logic needed to expose product operations.

The OpenAPI specification explains the underlying principle: a machine-readable description can represent an HTTP API's paths, operations, inputs, and responses. Generation is useful because it derives another interface from that contract.

Generation doesn't mean any installed binary knows every future endpoint. The generated client still has a version, and your GrowthBook server still has a version. A self-hosted instance can lag behind the public documentation. Treat API compatibility as a deployment fact you verify.

Skills provide the workflow guidance

GrowthBook's feature-flags skill routes requests to more specific workflows. Creating a flag, inspecting dependencies, changing targeting, requesting review, and publishing a revision are separate procedures.

That structure lets the agent load the guidance relevant to the current job. The skill authoring guidance on progressive disclosure supports this approach: keep the entry point focused and place detail in references that are loaded as needed.

The benefit is maintainability as well as context management. A correction to a flag workflow can be made in the maintained skill rather than repeated across a series of tool descriptions and client-specific prompts.

There are two shell concepts to keep distinct. The generated growthbook CLI is a terminal interface to the product API. The skills repository also includes a small gb-call helper for making REST requests. Installing a skill doesn't make that helper a globally available command; its location depends on the installation. Both can reach the API, but their configuration and invocation are different.

MCP provides a thin bridge

The current GrowthBook MCP implementation exposes four tools: growthbook_list_skills, growthbook_read_skill, growthbook_api_read, and growthbook_api_write.

An agent discovers a domain, reads the relevant workflow, then makes API calls. It doesn't need a dedicated MCP tool for every product endpoint. Calls described as gb-call GET in a skill map to the read tool; mutating methods map to the write tool with the same path and body.

The bridge does not run the shell helper. It forwards authenticated requests. Product-side permissions and validation remain important because a small tool surface can still reach many operations.

Shared guidance also has a delivery boundary: the MCP server bundles skills when it is built, using a pinned source revision. A newly edited skill in the repository needs to be included in a subsequent server build before that server supplies it. “Shared source” is a maintainability claim, not a promise of instant synchronization.

Explore the shared flag workflows

Open the feature-flags skill to see the procedures that guide creation, targeting, reviews, and publishing. Bring the same workflow knowledge to the agent interface your team uses.

View the Flag Skill

The same disabled flag can use either route

The practical question is whether the interface changes the job. Let's create a Boolean flag called checkout-redesign, with a false default and every environment disabled.

This is an API example for a sandbox project, not an application integration tutorial. It creates a control object; your application still needs a correctly configured GrowthBook SDK to evaluate it. The feature flag documentation covers the product concepts behind that integration.

Connect and verify before preparing the write

For the terminal route, install the current GrowthBook CLI, configure a Personal Access Token through its interactive setup, and inspect the available command syntax:

npm install -g growthbook
growthbook configure
growthbook whoami
growthbook features create --help
growthbook features get --help

Check that the active server and identity are the ones you intend to use. Prefer a tested, pinned CLI version in repeatable automation. Don't include a live token in a command you plan to share.

For an MCP route, the GrowthBook Cloud setup uses the hosted endpoint and browser OAuth. In a client using the documented mcpServers configuration shape, such as Cursor, add:

{
  "mcpServers": {
    "growthbook": {
      "url": "https://mcp.growthbook.io/mcp"
    }
  }
}

Complete the browser authorization and confirm tool discovery. Other clients can use a different configuration shape. Self-hosted GrowthBook users should follow the local stdio or self-hosted HTTP instructions rather than point a private instance at the Cloud service.

Next, let the connected agent discover the flag-creation workflow. These are tool-call parameters, shown separately in the order to invoke them:

{"name":"growthbook_list_skills","arguments":{}}

{"name":"growthbook_read_skill","arguments":{"name":"feature-flags"}}

{"name":"growthbook_read_skill","arguments":{"name":"feature-flags/references/flag-create"}}

The returned guidance should describe the prerequisites for creating the flag. If the workflow isn't present, resolve the server's bundled skill version before substituting instructions from an older integration.

Resolve real IDs and construct one payload

The flag-creation workflow checks existing keys, lists projects, and resolves environments. In the MCP client, invoke the read tool with each of these argument objects:

For the CLI route, perform that discovery with the corresponding command groups documented in the CLI command catalog:

growthbook features list-keys --output-format json
growthbook projects list --output-format json
growthbook environments list --output-format json

Inspect each command's help if your installed version differs. The returned keys, project IDs, and environment IDs are the inputs to the payload below. In MCP, the equivalent read-tool arguments are:

{"path":"/api/v2/feature-keys"}

{"path":"/api/v1/projects"}

{"path":"/api/v1/environments"}

Verify that checkout-redesign isn't taken, identify the sandbox project's ID, and enumerate every actual environment. These read responses determine the payload; don't treat example environment names as a complete inventory of your organization.

Save the following as flag.json, replacing <PROJECT_ID> and the environment keys with the discovered values. This example assumes the only environments are staging and production:

{
  "id": "checkout-redesign",
  "valueType": "boolean",
  "defaultValue": "false",
  "description": "Control exposure to the redesigned checkout",
  "project": "<PROJECT_ID>",
  "environments": {
    "staging": { "enabled": false },
    "production": { "enabled": false }
  }
}

The API represents defaultValue as a string, even for a Boolean flag. Explicitly disabling each environment avoids relying on the organization's default state for newly created flags. Use a PAT for this example so the caller has a user identity for attribution.

Review the permanent key, project, value, and disabled states before submitting. If the intended job is an experiment, route to experiment design first instead of creating an unrelated flag and hoping to connect it later.

Submit once, then read the object back

With the CLI, the create command accepts a JSON body. In a Bash-compatible shell, inspect the request with dry run before submitting:

growthbook features create --body "$(cat flag.json)" --dry-run
growthbook features create --body "$(cat flag.json)" --output-format json

The first command previews a request; it doesn't prove the server will accept it. Run the second only after checking the preview and approving this creation. In PowerShell, use that shell's file-reading syntax rather than paste the Bash substitution unchanged.

The PowerShell equivalent, using the same reviewed file, is:

$flagPayload = Get-Content -LiteralPath .\flag.json -Raw
growthbook features create --body $flagPayload --dry-run
growthbook features create --body $flagPayload --output-format json

The same distinction applies: preview first, approve the specific creation, then submit. Neither command changes the application's deployed code.

Through MCP, call growthbook_api_write with the same payload serialized into its body string. Substitute the same resolved project and environment names:

{
  "method": "POST",
  "path": "/api/v2/features",
  "body": "{\"id\":\"checkout-redesign\",\"valueType\":\"boolean\",\"defaultValue\":\"false\",\"description\":\"Control exposure to the redesigned checkout\",\"project\":\"<PROJECT_ID>\",\"environments\":{\"staging\":{\"enabled\":false},\"production\":{\"enabled\":false}}}"
}

Choose one creation route. Don't run both against the same key; they target the same product object, and the second creation should encounter an existing key.

Verify through the CLI get command:

growthbook features get --id checkout-redesign --output-format json

Or invoke growthbook_api_read with:

{"path":"/api/v2/features/checkout-redesign"}

Check the returned key, project, value type, default value, disabled state of every environment, and absence of unintended rules. Report those facts rather than “success.” No targeting or exposure change is included in this example.

Choose the route that fits the runtime

Once the procedure and API operation are shared, the remaining choice is operational. Where does the agent run? What can it execute? How does it authenticate? What does your team need to inspect afterward?

Shell access favors terminal composition

A shell-capable agent can run the CLI alongside repository tools, save structured output, and combine product inspection with local checks. That is useful when the job includes code changes, generated files, or a reproducible script.

For example, a flag audit can produce an inventory file while an engineer separately checks code references. The agent should preserve the association between the GrowthBook key and each repository reference. The final artifact can include both the product state and the proposed code diff.

The shell makes composition available; it doesn't make a workflow safe by default. A script can select the wrong profile or swallow an error. Decide which failures stop the workflow, where outputs are stored, and which steps need a reviewable artifact.

Remote tool access favors MCP clients

MCP is useful when the host already provides a tool connection but doesn't expose a terminal. A PM can inspect an experiment through a compatible assistant without installing a product CLI inside that assistant's runtime.

The MCP authorization specification defines an authorization framework for HTTP transports. GrowthBook Cloud uses browser OAuth, while local stdio configurations use credentials supplied to the process. Those are distinct deployment paths.

MCP also gives hosts a structured description of tools. The tool specification includes annotations such as read-only and destructive hints. Hosts can use those signals in their interaction design, but the signals are not an access-control boundary. The product must still enforce the caller's actual permissions.

Use a small decision table

Your immediate requirement	Route to consider	What to verify
Combine product operations with local files and scripts	CLI plus maintained skills	Shell access, profile, installed version, structured output
Connect a compatible assistant without a shell	Hosted MCP	HTTP/OAuth support, identity, tools, bundled workflow
Keep requests inside a self-hosted deployment	CLI or self-hosted MCP	Network reachability, server version, credentials, trusted app origin
Reuse a procedure across different team clients	Shared skills through either route	Workflow revision, API compatibility, expected review artifact

You can support more than one row. An engineer's CLI and a PM's MCP connection can operate on the same objects with different identities and permissions. Standardizing the workflow is often more useful than standardizing everyone's client.

Compare actual outcomes, not tool counts

Four MCP tools can address a large API. A large CLI command catalog can expose the same operations. Counting entries tells you little about whether an agent completed the intended job correctly.

Likewise, there is no universal token or speed result implied by the architecture. The client, model, instructions, response size, pagination, and number of requests all affect a real run. Measure the work you need instead of importing a result from an unrelated integration.

Keep the evaluation task constant

Use one sandbox project and one bounded task. For a read test, ask each route to find a named flag and identify its enabled environments, current revision, and relevant dependencies. For a write test, use separate temporary keys with the same reviewed disabled-flag requirements.

Give both runs the same expected output. Record whether each identified the correct objects, loaded the relevant workflow, handled missing data, and preserved the boundary between creation and exposure. Measure elapsed time and context consumption only alongside those correctness checks.

If one run gets rich workflow guidance and the other gets only a command name, you're testing the guidance as well as the interface. That can still be a useful product evaluation, but describe what changed.

Test failure behavior deliberately

Try a nonexistent object, an existing key, and a credential without the required permission. The agent should identify the failure and stop the dependent action. It should not invent an ID, silently pick another environment, or reinterpret a permission error as permission to retry with a broader credential.

The revision workflow adds another important test: multiple open drafts. When a chain of changes belongs in one revision, the agent must preserve its version rather than repeatedly ask for whichever draft is latest.

A creation receipt and a publication receipt are different artifacts. If your evaluation only checks that a request returned without error, it can miss the point where a proposed change became live or where a draft failed to include the intended edits.

Record the versions behind the result

Capture the CLI version, server version when available, client configuration, and the skill text or revision used. With MCP, inspect the guidance actually returned by the connected server. With installed skills, inspect the local instructions actually loaded.

That record makes a later regression diagnosable. A changed result may come from new guidance, a client update, a changed API, or different product state. “MCP became worse” is too broad to help you fix it.

Build workflows that survive the next client

The most useful consequence of GrowthBook's design is organizational. Engineers, PMs, and analysts can choose the agent surface that fits their work while referring to the same flags, experiments, and metrics.

An engineer can prepare a disabled flag from a terminal. A reviewer can inspect its draft in the app. An assistant connected through MCP can retrieve the same object and explain its state. The handoff should carry an ID, a revision where applicable, the proposed behavior, and the decision still required.

This is where the CLI-versus-MCP question loses much of its importance. Your release procedure doesn't need to be rewritten around each client. The product holds state; the API exposes operations; skills explain the work; the chosen interface delivers access.

Start with one inspection or sandbox creation. Require the agent to return a concrete object and its verified state. Then add the next workflow only when the current one is reliable enough for your team to review.

GrowthBook's feature flag platform gives that work a common place to live. The durable choice is how you connect release control and measurement to your team's process. CLI and MCP are ways to carry that process into the tools people already use.

Start with a common foundation

Set up GrowthBook for the flags, experiments, and metrics your agents will share. Then choose the CLI or MCP connection that fits each team member's work.

Get Started With GrowthBook

Experiments

Analytics

Standard deviation vs variance: Key differences for A/B testers

Oct 21, 2026

min read

A metric can have wide user-to-user variation and still yield a precise experiment estimate.

That is why confusing standard deviation with standard error creates bad A/B testing decisions. A dashboard may show that users differ substantially while the average effect is estimated closely enough to guide a release. Those statements can both be true.

Variance and standard deviation describe spread. Variance works on a squared scale; standard deviation takes its square root to return to the metric's original units. Neither is automatically the uncertainty around an experiment result.

For A/B testers, the useful distinction is practical: use standard deviation to communicate outcome variability, use variance in the calculations that combine uncertainty, and inspect the standard error or interval for the treatment effect. Start by making sure all three describe the correct unit of analysis.

Understand the difference in units

Variance uses squared distances

Outcomes above and below a mean have deviations with opposite signs. Simply averaging those signed deviations gives zero. Variance avoids that cancellation by squaring each deviation before combining them.

The sample variance formula is s² = Σ(xᵢ − x̄)² / (n − 1), where x̄ is the sample mean and n is the number of observations. The symbol Σ means to add the terms across observations.

If the outcome is measured in seconds, variance is measured in seconds squared. That is mathematically useful but less intuitive for explaining a product experience. “Variance is 4 seconds squared” does not mean users differ by 4 seconds.

Standard deviation returns to the original scale

Standard deviation is s = √s². A variance of 4 seconds squared corresponds to a standard deviation of 2 seconds. Both describe the same dispersion, expressed on different scales.

Do not define standard deviation as the average absolute distance from the mean. That is a different measure. Squaring deviations gives large deviations more influence, and taking the square root afterward does not undo that weighting.

Quantity	What it describes	Units for task time
Variance	Squared dispersion in outcomes	Seconds squared
Standard deviation	Outcome dispersion on the original scale	Seconds
Standard error of the mean	Sampling variability of an estimated mean	Seconds

Neither variance nor standard deviation requires a normally distributed population merely to be calculated. Normality matters for particular interpretations and inferential procedures, not for the existence of these summaries when the required moments are finite.

Calculate both from the same observations

Work through a small dataset

Use four synthetic task times: 2, 4, 4, and 6 seconds. This tiny dataset is for arithmetic, not evidence about a real product or a basis for confident inference.

The mean is (2 + 4 + 4 + 6) / 4 = 4 seconds. Deviations from the mean are −2, 0, 0, and 2 seconds. Their squares are 4, 0, 0, and 4 seconds squared, totaling 8.

Treating these observations as a sample, the usual sample variance is 8 / (4 − 1) = 8/3, or about 2.667 seconds squared. The sample standard deviation is √(8/3), or about 1.633 seconds.

This is a useful check on a report. If someone describes the same sample's variance as 1.633, they have probably substituted the standard deviation. If the units are missing, the mistake is much harder to spot.

Choose sample or population formulas deliberately

If those four observations constitute the entire finite population you want to describe, population variance divides by 4: 8/4 = 2 seconds squared. Population standard deviation is √2, or about 1.414 seconds.

The population and sample distinction depends on what you are estimating. Having every recorded event from an experiment does not necessarily make those events the full population of future users or future conditions you care about.

The n − 1 denominator makes the usual sample variance an unbiased estimator of population variance under independent, identically distributed sampling with finite variance. It does not make the square root exactly unbiased for population standard deviation. Nor does it correct biased sampling or dependence between observations.

Verify the calculation with explicit function names

Python's statistics functions distinguish sample calculations from population calculations. With Python 3 installed, this standalone example requires no external packages or data:

from statistics import variance, stdev, pvariance, pstdev

times = [2, 4, 4, 6]
print(round(variance(times), 3), round(stdev(times), 3))
print(round(pvariance(times), 3), round(pstdev(times), 3))

The first line of output is 2.667 1.633; the second is 2 1.414. The different denominators explain the difference. Before comparing statistics from two tools, check their sample/population defaults and handling of missing values.

Find the noise you can reduce

Explore practical variance reduction methods, including metric design and CUPED, and the conditions that make each approach useful.

Read the Variance Reduction Guide

Use standard errors for experiment uncertainty

Distinguish users from estimated means

Standard deviation describes how users' outcomes vary. Standard error describes how an estimator would vary across repeated samples. For an independent sample, the estimated standard error of its mean is s / √n.

Suppose a user-level task-time metric has a sample standard deviation of 20 seconds among 10,000 independent users. The estimated standard error of the mean is 20/√10,000 = 0.2 seconds. Large differences between users coexist with a much smaller uncertainty around their average.

Collecting four times as many independent users would halve this standard error if the outcome variance stayed similar. It would not mechanically halve user-level standard deviation. The individual experience remains variable even as the estimated mean becomes more precise.

Combine arm variances before taking the square root

For independent treatment and control groups, a simple unadjusted difference in means has estimated variance s²ₜ/nₜ + s²꜀/n꜀. Its standard error is the square root of that sum. You do not add the two arm standard deviations and call the result the experiment's uncertainty.

Take a separate synthetic summary with 10,000 independent users in each arm and a 20-second standard deviation in both. The variance of the estimated difference is 400/10,000 + 400/10,000 = 0.08 seconds squared. Its standard error is √0.08, about 0.283 seconds.

If the observed treatment-minus-control difference is −1 second, an illustrative large-sample, unadjusted 95% normal interval is −1 ± 1.96 × 0.283, approximately −1.554 to −0.446 seconds. Negative values mean faster completion under this metric definition.

This example assumes independent groups and an appropriate large-sample approximation. It is not the exact output of GrowthBook's relative-lift, sequential, covariate-adjusted, or ratio-metric methods. GrowthBook's statistical details describe how the platform estimates effects and their uncertainty.

Avoid interpreting intervals as outcome ranges

That interval concerns the mean treatment effect. It does not say that 95% of individual users improved by between 0.446 and 1.554 seconds. An individual user's causal effect is a different quantity, and the experiment does not observe both potential outcomes for the same person.

Likewise, mean ± one standard deviation is not a universal statement about where 68% of users fall. That familiar interpretation depends on an approximately normal distribution. Skewed task times or revenue can look very different.

The frequentist confidence level describes the repeated-sampling coverage of the interval procedure under its assumptions. It is not a posterior probability assigned to a fixed realized interval.

Check what your metric actually measures

Match the variance to the randomization unit

If users are randomized and each contributes many requests, request rows are not automatically independent experimental units. Treating 100 requests from one person as 100 unrelated users can make uncertainty look smaller than it should.

Define the outcome at the intended unit or use a method that accounts for clustering. GrowthBook's aggregate data requirements are relevant when supplying precomputed summaries: the sample size, sum, and dispersion must correspond to the statistic and analysis method.

Two teams can report different standard deviations without either making an arithmetic mistake. One may summarize per-request latency while the other summarizes each user's average latency. They are describing different outcome distributions. Clarify the grain before comparing their numbers.

Paired measurements need another distinction. If the same users provide before-and-after outcomes, the measurements within each pair can be correlated. Analyze each user's difference or use an appropriate paired method; do not apply the independent-arm formula automatically. The paired-means framework treats those differences as the observations of interest. Pairing also does not remove time trends or establish causality by itself; the design still determines which comparison is defensible.

Inspect tails instead of deleting them casually

Large observations influence both variance and standard deviation. A few unusually long tasks can dominate a time metric; a few large purchasers can dominate revenue. Determine whether those values reflect valid behavior, instrumentation defects, retries, or unit errors.

A valid expensive user is not automatically an outlier to discard. Removing high values after seeing an experiment result can change the estimand and introduce selective analysis. Decide justified exclusions or transformations before interpreting the test.

Report complementary summaries when they answer useful questions: a histogram, median, or a relevant tail percentile can show what a single spread measure hides. Those summaries do not replace the mean effect if the mean remains the decision metric.

Keep units consistent across pipelines

Converting seconds to milliseconds multiplies every value by 1,000. Standard deviation also multiplies by 1,000, but variance multiplies by 1,000,000. A dramatic numerical variance increase can therefore be a unit conversion rather than a product regression.

For the four-value example, sample standard deviation becomes approximately 1,633 milliseconds and variance becomes approximately 2,666,667 milliseconds squared. The underlying task times have not changed. Store units with metric definitions and inspect them when comparing dashboards.

A lower variance caused solely by rescaling a metric does not create more statistical information. The effect size rescales too. Separate a numerical change in units from an actual improvement in the precision of your estimate.

Also avoid averaging standard deviations from daily reports and labeling the result a weekly standard deviation. The complete-period spread depends on both variation within days and differences between daily means. Keep the underlying observations or sufficient summaries that support the intended calculation. A simple average of displayed daily values generally loses information needed to reconstruct the full distribution.

Turn spread into a better testing plan

Define the outcome before planning the sample

Start with the metric definition: population, identity, aggregation, window, units, exclusions, and desired effect. Estimate variability from representative historical data at that same grain.

Historical variance is an input, not a guarantee. New traffic, a different user mix, or a changed measurement window can alter it. Explore plausible variance and effect-size assumptions rather than treating one historical number as exact.

Keep the two arm variances separate when appropriate. A treatment can change variability as well as its mean. The simple equal-standard-deviation illustration above is a teaching assumption, not a requirement that production groups have identical spread.

Reduce estimation noise without hiding behavior

CUPED and post-stratification use suitable pre-experiment information and covariates to improve effect estimation. CUPED stands for Controlled-experiment Using Pre-Experiment Data. Its value depends on useful predictive information and a valid implementation.

Adjustment can reduce uncertainty in the treatment effect without making real users' outcomes less variable. That distinction prevents a reporting error: a narrower adjusted interval is not evidence that customers now experience a more consistent product.

Also separate missing data from genuine zeros. A user with no purchase may correctly contribute zero revenue; a missing instrumentation event might represent an unknown outcome. Treating both identically can distort the mean and its variance before any statistical engine sees the data.

Report the right quantity for the decision

Reader's question	Useful quantity
How much do individual outcomes differ?	Standard deviation, with distribution context
What enters this uncertainty calculation?	Variance at the correct analysis unit
How precisely is the effect estimated?	Standard error and an appropriate interval
Is the measured difference worth acting on?	Effect size, uncertainty, guardrails, and decision context

For a clear experiment readout, show the metric's unit and analysis grain, the estimated effect, and its appropriate uncertainty interval. Add outcome spread when it helps readers understand the population or diagnose a noisy metric.

GrowthBook's experimentation platform brings defined metrics and statistical analysis together. A trustworthy interpretation still starts with your measurement choices: describe spread with standard deviation, calculate with variance where required, and judge precision using the estimator's uncertainty.

Build a clearer experiment readout

Connect your metrics to GrowthBook and evaluate effects with the analysis method and measurement definitions your team has chosen.

Get Started With Experimentation

Experiments

Analytics

How to calculate true positive rate (TPR)

Oct 21, 2026

min read

Catching 80 defects means little until you know how many defects existed.

Suppose a detector flags 125 suspicious software changes. Engineers inspect them and confirm 80 real defects. That tells you something about alert quality, but it does not tell you how many defects the detector missed. To calculate true positive rate, you need the actual positives outside the alert queue too.

True positive rate, or TPR, measures the share of actual positive cases that a system correctly identifies. It is also called recall or sensitivity. The formula is TP / (TP + FN), where TP means true positives and FN means false negatives.

The arithmetic is simple. Choosing the right population, labels, threshold, and denominator is the difficult part. This guide works through an engineering example, distinguishes neighboring metrics, and explains what changes when the “test” is an A/B experiment rather than an item classifier.

Start with actual positives, not alerts

Define the positive class

“Positive” means the condition you want to detect. It does not necessarily mean a good outcome. In a defect detector, positive means a real defect. In a spam filter, it means spam. Write that definition before calculating anything.

A true positive is an item that is actually positive and predicted positive. A false negative is actually positive but predicted negative. Those two groups together form the denominator: all actual positives in the evaluation sample.

The recall definition is therefore conditional on actual class membership. TPR asks, “Among the real defects, what proportion did we catch?” It does not ask, “Among the alerts, what proportion were real?”

Fix the unit and observation window

Choose a consistent evaluation unit. A code change, an individual finding, and a repository are different units. If one change generates 12 duplicate alerts, counting alerts in the numerator and changes in the denominator produces a meaningless rate.

For the example, each unit is one code change, evaluated once by one fixed detector version at one fixed threshold. An independent review process eventually labels each change as defective or not defective. The observation window is long enough for those labels to mature.

This resembles the discipline needed when defining experiment metrics: the event, identity, time window, and denominator must describe the same question. A correct formula applied to incompatible counts still gives the wrong answer.

Calculate TPR from the confusion matrix

Put every evaluated item in one cell

Consider an original synthetic evaluation of 1,000 code changes. Reviewers establish that 100 contain a defect and 900 do not. The detector catches 80 defects, misses 20, and incorrectly flags 45 nondefective changes.

Actual label	Predicted positive	Predicted negative	Total
Defective	80 true positives	20 false negatives	100
Not defective	45 false positives	855 true negatives	900
Total	125	875	1,000

Read the labels rather than relying on cell position. Libraries and reports can arrange axes differently. The scikit-learn confusion matrix convention uses actual classes on rows and predicted classes on columns, with class order also affecting where each value appears.

Check the totals before calculating rates. The four cells sum to 1,000. True positives plus false negatives sum to 100 actual defects. Predicted positives total 125, which is a different denominator.

Divide detected positives by all actual positives

The calculation is:

TPR = TP / (TP + FN) = 80 / (80 + 20) = 80 / 100 = 0.80 = 80%.

Interpret it in words: the detector caught 80% of the actual defects in this evaluation sample. It missed 20%, so the false negative rate is 20%. For a binary task with complete labels, TPR and false negative rate sum to 100%.

Do not divide 80 by 1,000. That would measure true positives as a share of all evaluated changes, not recall. Do not divide 80 by 125 either. That is precision, which answers the alert-quality question.

The result describes this sample and threshold. It does not establish that every future workload will have the same recall, or that all defect categories are equally detectable. Keep the counts beside the percentage so readers can see the support behind it.

Handle zero positive support explicitly

If the sample contains no actual defects, TP + FN equals zero. Sample TPR is undefined. Returning 0% would imply the detector missed known defects; returning 100% would imply it successfully found them. Neither interpretation is supported.

Software libraries need a practical zero-division convention. That convention can return a placeholder or warning, but it does not create evidence. Report “TPR unavailable: zero actual positives” and preserve the support count. A pipeline can then distinguish an unevaluable slice from measured poor performance.

Check the experiment error risks

See how power, repeated checks, and multiple comparisons affect the reliability of experimental decisions beyond a single classifier score.

Read the False Positives Guide

Compare TPR with precision and false positives

Keep the denominators visible

For the same 1,000 changes, the other common metrics tell different stories:

Metric	Calculation	Result
True positive rate / recall	80 / 100 actual positives	80%
Precision	80 / 125 predicted positives	64%
False positive rate	45 / 900 actual negatives	5%
Specificity	855 / 900 actual negatives	95%
Accuracy	(80 + 855) / 1,000 changes	93.5%

The classification metric definitions differ because they condition on different populations. Here, 36% of alerts are false, but the false positive rate is 5%. Calling both numbers “the false positive rate” hides the operational distinction.

Accuracy can also look reassuring in an imbalanced population. A detector that labels all 1,000 changes nondefective would be 90% accurate while detecting none of the 100 defects. TPR exposes that failure, though it still needs the false-positive side of the picture.

Choose a threshold for the decision

Suppose a stricter threshold, evaluated on the same labeled changes, catches 60 defects and incorrectly flags 10 nondefective changes. Its TPR is 60%, its precision is about 85.7%, and its false positive rate is about 1.11%.

This threshold reduces the review queue from 125 changes to 70. It also misses 40 defects instead of 20. Whether that tradeoff is acceptable depends on the consequences of a missed defect, the review team's capacity, and what action follows an alert.

A ROC curve plots TPR against false positive rate across thresholds. It helps compare operating points. It does not pick the operational threshold for you, and an area-under-curve summary does not specify the queue size at the threshold you intend to deploy.

If you tune thresholds using the same labels you later report as a final evaluation, the score can be optimistic. Use separate validation and held-out evaluation data, or another defensible evaluation design, and freeze the decision rule before the final assessment.

Specify the action at each threshold too. A low-confidence finding might create a suggestion, while a high-confidence finding might block a merge. Those are different interventions with different error costs. One aggregate recall figure should not imply that every detected item received the same treatment.

Make sure the labels can support the claim

Audit predicted negatives too

If engineers review only alerts, you can estimate precision within the reviewed alert population. You cannot directly count missed defects among unreviewed negatives. Assuming those changes are clean makes FN artificially small and TPR artificially high.

An evaluation may need independent review of a representative sample of predicted negatives, delayed incident labels, or a curated benchmark with known defects. Each approach has limits. Incident labels miss undetected failures; curated examples can differ from ordinary production work.

If the evaluation oversamples suspicious changes or certain repositories, report that design. Use appropriate weighting when estimating performance for the real workload. A simple unweighted confusion matrix describes the sampled dataset, which may not represent the deployed population.

Preserve uncertainty and segment support

An 80% estimate based on 4 detected defects out of 5 is much less precise than one based on 800 out of 1,000. The important sample size for recall is the count of actual positives, not just the total number of changes evaluated.

Report positive support by important slices, such as language, defect category, or repository type. A high pooled TPR can hide weak performance on a rare but expensive failure mode. At the same time, avoid declaring tiny slices definitively better or worse from a few examples.

Counts alone do not make observations independent. Many similar changes from one repository can share a common pattern. Use uncertainty methods that fit the evaluation design rather than assuming every row is an unrelated trial.

Separate label delay from label absence

A recently deployed change might appear nondefective because nobody has had time to find the bug. Treating it as a confirmed negative gives the newest cohort a different labeling standard from older cohorts.

Define when an item becomes eligible for evaluation and track unresolved labels separately. Keep model version, threshold, label version, and observation dates with the result. That makes a later score change interpretable: you can tell whether the detector changed, the workload changed, or the labels matured.

For a warehouse-native measurement workflow, these definitions belong in the underlying data model. Joining model decisions to review outcomes still requires identity and time alignment; a queryable warehouse does not automatically resolve ambiguous ground truth.

Keep comparable populations together

When comparing detector versions, evaluate them on the same held-out cases where possible. Otherwise, an apparent recall improvement could come from an easier mix of defects. Preserve a breakdown of new, removed, and unchanged cases so reviewers can see what changed between evaluations.

When combining reports, add the underlying TP and FN counts for nonoverlapping, consistently defined populations, then calculate the pooled rate. An unweighted average of repository percentages answers a different question because it gives a tiny repository the same influence as a large one. Either summary can be useful, but label the weighting explicitly.

If the same change appears in several reports, deduplicate or model that repeated observation before pooling. Repeated scans do not create additional independent defects. Keep an audit trail from the final counts back to the evaluated item identifiers so a suspicious rate can be investigated.

Connect detection quality to product decisions

Distinguish classifier recall from statistical power

In hypothesis testing, statistical power is the probability that a testing procedure rejects the null when a specified alternative is true. It is a repeated-test detection probability, depending on assumptions such as effect size, variance, sample size, and decision rule.

That is related to the idea of detecting a real signal, but it is not the same dataset as a labeled-item confusion matrix. In an ordinary A/B program, you do not observe the true causal effect of every experiment with certainty. Dividing declared winners by all experiments does not reveal a ground-truth TPR.

Power planning asks how often your procedure would detect a particular real effect under its assumptions. A classifier evaluation asks how many labeled positives were detected in the evaluated sample. Keep those questions separate when discussing GrowthBook's statistical methods.

Evaluate the intervention as well as the detector

An improved offline detector can still create a worse product workflow. More alerts might overwhelm engineers, delay releases, or catch defects too late to matter. Conversely, a modest recall change might be valuable if it catches the failures with the highest operational cost.

When appropriate, use randomized experiments to evaluate the downstream intervention: which review experience helps teams resolve defects, with what delay and cost? Keep detector recall, review workload, and product outcomes as separate measures.

GrowthBook's experimentation platform can analyze defined outcomes from such tests. Your team supplies reliable assignment, exposure, labels, and metric definitions. Neither a high TPR nor a significant product result eliminates the need to inspect the other evidence.

Use a repeatable reporting checklist

Before sharing a TPR number, state the positive class, evaluation unit, detector version, threshold, and label process. Show TP and FN beside the rate. Include precision or false positive rate so readers can assess the workload created by detection.

Then ask whether predicted negatives were evaluated, whether labels had time to mature, and whether the sample reflects the population where you will act. Mark zero-support slices unavailable and explain material gaps in coverage.

The useful result is a statement someone can audit: “At this threshold, the detector found 80 of 100 labeled defects in these 1,000 evaluated changes, while producing 45 false alerts.” That is a clearer basis for a decision than “our model is 80% accurate.”

Measure what the change delivers

Connect your data and defined metrics to GrowthBook to evaluate how a product or workflow change affects the outcomes your team cares about.

Start Measuring With GrowthBook

Ready to ship faster?

No credit card required. Start with feature flags, experimentation, and product analytics—free.

Get Started

Book a Demo

Simplified white illustration of a right angle ruler or carpenter's square tool.

White checkmark symbol with a scattered pixelated effect around its edges on a transparent background.

Scoring each step of an agent workflow and calling it an experiment is like grading every sentence in a report without checking whether the report answered the question.

Why AI agent experiments are fundamentally different from prompt A/B tests

What traditional prompt A/B tests actually measure

Why agents break the assumptions that make prompt A/B tests valid

The cascade failure problem

The evaluation unit must be the workflow

The four metrics that expose what step-level scoring misses in agent workflows

Task-completion rate: the primary signal

Error recovery rate: measuring resilience under failure

Step efficiency: the cost hidden in the decision path

Failure point attribution: finding where workflows actually break

Mapping workflow metrics to business outcomes

Structuring AI agent experiments around tool use, error recovery, and task completion

Isolating the experimental variable in a multi-component agent system

Feature flags as the mechanism for switching agent configurations without a deploy

Treating architectural decisions as testable hypotheses

Running controlled rollouts at the workflow level

The hard problems in AI agent experiments: non-determinism, long horizons, and attribution

The non-determinism problem — why agent experiments have a higher noise floor

Long-horizon observation windows — how task duration distorts experiment timing

Attribution across multi-step workflows — which decision caused the outcome?

Replay-based testing environments — controlling for non-determinism

Building a continuous improvement loop for AI agent workflows

Establishing a baseline and iteration cadence

Documenting experiments as learning artifacts

Tracking cumulative workflow-level impact

Three starting points for teams that have never run a controlled agent experiment

Related insights

Sign up for free

Table of Contents

Related Articles

CLI vs MCP: TLDR, it doesn’t matter as much as you think

Your agent should know how to do the job whichever interface it uses.

The debate combines three different questions

How can the agent reach the product?

What procedure should the agent follow?

What context makes the procedure relevant?

GrowthBook puts the durable parts below the interface

The API provides the operations

Skills provide the workflow guidance

MCP provides a thin bridge

Explore the shared flag workflows

The same disabled flag can use either route

Connect and verify before preparing the write

Resolve real IDs and construct one payload

Submit once, then read the object back

Choose the route that fits the runtime

Shell access favors terminal composition

Remote tool access favors MCP clients

Use a small decision table

Compare actual outcomes, not tool counts

Keep the evaluation task constant

Test failure behavior deliberately

Record the versions behind the result

Build workflows that survive the next client

Start with a common foundation

Standard deviation vs variance: Key differences for A/B testers

A metric can have wide user-to-user variation and still yield a precise experiment estimate.

Understand the difference in units

Variance uses squared distances

Standard deviation returns to the original scale

Calculate both from the same observations

Work through a small dataset

Choose sample or population formulas deliberately

Verify the calculation with explicit function names

Find the noise you can reduce

Use standard errors for experiment uncertainty

Distinguish users from estimated means

Combine arm variances before taking the square root

Avoid interpreting intervals as outcome ranges

Check what your metric actually measures

Match the variance to the randomization unit

Inspect tails instead of deleting them casually

Keep units consistent across pipelines

Turn spread into a better testing plan

Define the outcome before planning the sample

Reduce estimation noise without hiding behavior

Report the right quantity for the decision

Build a clearer experiment readout

How to calculate true positive rate (TPR)