MEnvAgent: Scalable Polyglot Environment Construction for Verifiable Software Engineering

🎯 Pitch

Building a single software environment is hard; building thousands across 10 languages to test AI coders is a bottleneck that's been holding back execution-based verification. MEnvAgent automates this with a multi-agent loop that diagnoses its own build failures and a reuse mechanism that patches old environments instead of starting fresh, cutting time costs by 43% while improving reliability—and the resulting polyglot dataset boosts coding agent performance across the board.

1. Executive Summary

This paper introduces MEnvAgent, a multi-language framework that automates the construction of executable Docker environments for verifiable software engineering tasks, targeting the bottleneck of manually building environments across diverse programming languages. Evaluated on MEnvBench — a new benchmark of 1,000 tasks spanning 10 languages — MEnvAgent employs a Planning-Execution-Verification multi-agent architecture to autonomously diagnose and resolve build failures, paired with a novel Environment Reuse Mechanism that adapts historical environments via incremental patching rather than rebuilding from scratch. The framework improves Fail-to-Pass (F2P) rates by 8.6% while reducing time costs by 43% against state-of-the-art baselines, and its utility is validated by constructing MEnvData-SWE — the largest open-source polyglot dataset of verifiable Docker environments — whose solution trajectories yield consistent performance gains on SWE-bench across multiple model sizes, establishing that scalable execution-based verification can push the boundaries of coding agents only when environment construction is automated with reuse-driven efficiency.

2. Context and Motivation

The Core Problem: Environment Construction Is the Bottleneck for Verifiable SWE

Modern software engineering benchmarks — particularly those based on real-world GitHub issue resolution like SWE-bench and its variants — have elevated the standard for evaluating LLMs' coding capabilities by requiring execution-based verification: an agent's proposed fix must actually compile, install, and pass tests within a live environment. This is a fundamentally different evaluation paradigm from static code comparison, and it has driven the development of autonomous coding agents like OpenHands and SWE-Agent that explore repositories, localize bugs, and generate patches that are validated by actually running the project's test suite.

But this execution-based standard creates a dependency that the paper identifies as the field's central bottleneck: before you can evaluate an agent on a repository, you must construct a working, executable environment for that repository at a specific historical snapshot. This is the "environment construction" problem, and the paper argues it is the primary constraint on scaling verifiable software engineering data.

Why is this hard? The paper identifies two tightly coupled challenges:

Complexity. Real-world repositories are not standardized. Each has its own language, build system, dependency graph, package manager, and test framework — often with implicit assumptions about system libraries, environment variables, and toolchain versions. A Python project might use pip, poetry, or conda; a Java project could require Maven or Gradle; C/C++ projects involve CMake with compiler-specific flags. Getting any single environment to build is a non-trivial exercise in dependency resolution. Getting it to build correctly at a historical snapshot — where package registries may have changed, deprecated APIs may have been removed, and the original build environment is no longer available — multiplies the difficulty. The paper explicitly notes that "frequent construction failures (e.g., version conflicts, compilation errors) and inconsistent testing protocols (e.g., pytest or mvn test) often lead to low success rates" (Section 1).
Time Consumption. Building environments from scratch is inherently slow: downloading dependencies, compiling code, and running installation scripts can take minutes to hours per repository. Worse, these environments are fragile. A single misconfigured command or version mismatch can make the entire build state invalid, and the typical recovery strategy is a "clean-slate restart" — throw everything away and start from a fresh base image. This makes large-scale data expansion computationally prohibitive. The paper characterizes this as a "prohibitive overhead for large-scale data expansion" (Section 1).

The consequence of these twin challenges is a scalability dilemma that the paper frames explicitly. On one end of the spectrum, there are approaches that scale efficiently but provide only approximate verification: methods based on static code metrics can process thousands of repositories quickly but cannot actually run the tests, so they produce training signals that are noisy or unreliable. On the other end, manual environment construction (as practiced in SWE-gym) produces high-quality, genuinely verifiable environments but is labor-intensive — requiring human experts to configure each repository individually — and has been "largely restricted to Python" (Section 1). There is a "critical gap for scalable, verifiable support across diverse programming languages" (Section 1).

Why This Problem Matters: Training, Evaluation, and the RLVR Paradigm

The paper's motivation extends beyond benchmarking to the rapidly emerging paradigm of Reinforcement Learning with Verifiable Rewards (RLVR). In RLVR, an LLM agent generates code changes, executes them in an environment, and receives a binary reward based on whether the tests pass — a clean, objective signal that has proven highly effective for training reasoning capabilities. The paper cites Wen et al. (2025) to establish that "execution-based verification is pivotal, not only for evaluation but also for emerging training paradigms like RLVR."

But RLVR's effectiveness is "constrained by the scalability of executable environment construction" (Section 1). If you can only build environments for a few hundred Python repositories, your RLVR training pipeline is capped at that scale. To unlock RLVR's full potential — and to enable training on the diversity of problems that real software engineering entails — you need a way to automatically construct executable environments at scale across many languages. This is the practical urgency behind the paper.

The problem also has downstream consequences for the entire SWE evaluation ecosystem. As the paper notes in Appendix A, benchmarks like SWE-bench Multilingual, Multi-SWE-bench, and SWE-bench Multimodal all depend on being able to construct environments for their evaluation instances. If environment construction remains a manual bottleneck, these benchmarks cannot easily expand to cover new languages, new repositories, or new task types — they stagnate on whatever environments human curators have had time to build. The paper explicitly positions MEnvAgent as infrastructure that "can significantly accelerate this process, enabling the continuous update of these benchmarks with fresh, real-world repositories to prevent data contamination and stagnation" (Appendix A.1).

Where Prior Approaches Fall Short

The paper surveys two categories of prior work and identifies specific limitations in each.

Automated environment construction methods. These fall into two generations. First-generation approaches used static heuristics to infer dependencies from source code — regex-based parsing of requirements.txt, pom.xml, CMakeLists.txt, and so on. While deterministic and fast, these methods "struggl[e] with complex configurations and version incompatibilities" (Section 7). Real-world repositories don't always declare their dependencies cleanly or completely; undocumented system-level requirements (e.g., a specific C library that must be apt-get installed before pip install will work) are invisible to static analysis.

Second-generation approaches leverage LLMs but exhibit their own limitations:

Repo2Run employs a dual-agent framework but is "tailored with Python-specific tools, focusing exclusively on environment installation via fixed test commands that do not execute verification tests" (Section 7). It handles only Python and skips the critical F2P verification step — meaning it might produce environments that technically install but don't actually reproduce the bug the agent is supposed to fix.
SWE-Bench-Live extends to both environment setup and test configuration but uses a "single-agent method via interactive bash sessions" — a simpler architecture that lacks the specialized diagnosis and refinement loops that the paper argues are necessary for high success rates.
SWE-Factory is the most competitive baseline, supporting four languages and introducing multi-agent collaboration. However, its trial-and-error approach is inefficient — the paper's experiments show it "suffers from excessive latency due to inefficient trial-and-error loops" (Section 5 results discussion), clustering in the high-time-cost region of the performance scatter plot.

None of these approaches incorporates an environment reuse mechanism. Every method rebuilds environments from a base image, paying the full cost of compilation and dependency resolution even when a nearly-identical environment already exists for a different version of the same repository. This is the key efficiency gap the paper identifies.

Environment construction benchmarks. The paper catalogs a progression of benchmarks (Section 7) and identifies a consistent pattern of tradeoffs:

Early benchmarks (SUPER, CORE-bench, ML-bench) evaluated environment construction only implicitly as part of larger tasks, making it impossible to isolate and study the construction challenge itself.
INSTALLAMATIC and EXECUTIONAGENT established rigorous execution-based evaluation but remained small-scale — useful for measuring capability but not for driving large-scale data generation.
EnvBench and Repo2Run-bench scaled up data volume but "relied on approximate evaluation metrics like static compilation checks or test collection, which often fail to detect runtime incompatibilities essential for robust agent feedback" (Section 7). A project might compile cleanly but crash at runtime due to a missing shared library — a failure invisible to static checks.
EnConda-Bench added process-level diagnostics but "remains restricted to Python and rigid configuration patterns."
SweSetupBench-lite (from SWE-Factory) aligns evaluation with realistic software evolution by using historical snapshots and F2P metrics, but its "representativeness of the benchmark is hindered by a limited scope of just 12 repositories" (Section 7).

The consistent pattern across all existing environment construction benchmarks is a trade-off between quality (execution-based verification, broad language coverage, diverse repositories) and scale (number of tasks). No benchmark simultaneously achieves broad polyglot coverage, strict execution-based F2P evaluation with quality assurance, and representative repository diversity. MEnvBench is explicitly designed to occupy this gap — 10 languages, 200 repositories, 1,000 tasks, strict F2P evaluation — as detailed in Table 1.

How MEnvAgent Positions Itself

The paper's framing is not that environment construction is an unsolved problem — prior tools can and do build environments — but rather that existing solutions fail to simultaneously achieve high success rates, broad language coverage, and computational efficiency. The paper positions MEnvAgent as addressing this trilemma through two architectural innovations, each mapped to one of the two bottleneck challenges:

For the complexity challenge: a multi-agent Planning-Execution-Verification loop (Section 3.1). Rather than a monolithic agent that tries to generate a complete build script in one shot, MEnvAgent decomposes the task across specialized agents — Repository Analysis, Environment Setup, Test Configuration, Environment Execution, and Verification — that operate in an iterative closed loop. When the Verification Agent detects a failure, it performs error attribution (diagnosing whether the failure is a missing dependency or an incorrect test command) and feeds that diagnosis back to the Planning Stage for a targeted retry. This architecture is designed to autonomously resolve the "version conflicts, compilation errors, and inconsistent testing protocols" that prior single-pass approaches cannot handle.

For the time consumption challenge: an Environment Reuse Mechanism (Section 3.2). This is the paper's most distinctive contribution. Rather than treating each environment construction task as independent, MEnvAgent maintains a pool of previously verified environments. When a new task arrives, it retrieves the most similar historical environment — using a hierarchical strategy based on version consistency and backward compatibility — and attempts to patch it incrementally rather than rebuilding. A dedicated EnvPatchAgent generates a minimal sequence of commands ( $\Delta\mathcal{P}$ ) that adapts the retrieved environment to the target repository snapshot. The paper frames this as solving an optimization problem: find $S_{sim}$ that minimizes expected adaptation cost, then synthesize $\Delta\mathcal{P}$ such that the patched environment satisfies the F2P criterion. The key insight is that software evolution is incremental — a newer version of a repository shares most of its environment with an older version — so rebuilding from scratch is wasteful when only a delta needs to be applied.

The paper explicitly connects this work to the broader ecosystem of verifiable SWE datasets (Appendix A.2), positioning MEnvAgent as orthogonal and complementary to approaches like SWE-Smith (which generates synthetic bugs in pre-built environments) and SWE-Flow (which synthesizes tasks from unit tests). MEnvAgent provides the foundational infrastructure — a large pool of successfully built environments — that these other methods could use as their starting point, amplifying their own generation pipelines.

Finally, the paper distinguishes itself through its end-to-end validation approach. Rather than stopping at a benchmark evaluation, it uses MEnvAgent to construct MEnvData-SWE — 3,005 task instances from 942 repositories — and demonstrates that fine-tuning on trajectories from this dataset produces consistent, substantial gains on SWE-bench across five different model architectures. This closes the loop: the environment construction framework isn't just a tool for evaluation; it's infrastructure that directly improves the state of the art in software engineering agents.

3. Technical Approach

3.1 Reader Orientation

MEnvAgent is an automated framework that takes a GitHub repository at a specific historical commit, analyzes its codebase, and builds a fully functional Docker container where the repository's test suite can be executed — a task that traditionally requires human experts to manually resolve dependency conflicts, configure build systems, and debug installation failures across diverse programming languages. The system solves the environment construction problem by orchestrating multiple specialized LLM agents in a closed-loop architecture where failures in building or testing are automatically diagnosed and used to refine the construction plan, while simultaneously avoiding redundant work by recognizing when a previously-built environment for the same repository can be incrementally patched rather than rebuilt from scratch.

3.2 Big-Picture Architecture (Diagram in Words)

The MEnvAgent framework has two major operational phases and five specialized agent roles:

Phase 1: Environment Reuse. Before any new construction begins, the system queries an Environment Pool (a database of previously verified Docker environments, each tagged with its repository and version) to find a historical environment that is similar to the target repository snapshot. A dedicated EnvPatchAgent attempts to adapt this retrieved environment by generating a minimal sequence of shell commands that updates it to match the target state. If this succeeds, the environment is reused immediately with a fraction of the computational cost of a full build.

Phase 2: Iterative Construction. If reuse fails or no similar environment exists, the system enters a Planning-Execution-Verification loop involving five agents:

Repository Analysis Agent — surveys the repository's file structure, identifies the programming language, build system, dependency declarations, and entry points, and produces a structured summary.
Environment Setup Agent — consumes this summary and selects a base Docker image, then generates a complete installation script (the build process $\mathcal{P}$ ) containing all dependency installation and configuration commands.
Test Configuration Agent — analyzes the repository and the proposed installation script to determine how to apply the test patch and which test command to invoke (e.g., pytest tests/, mvn test, go test ./...).
Environment Execution Agent — instantiates a Docker container from the selected base image, executes the installation script, monitors terminal output in real-time, and can dynamically adjust commands to resolve immediate errors (e.g., installing a missing system package). If installation fails irrecoverably, it aborts and returns control to the Planning Stage.
Verification Agent — runs the test suite inside the constructed environment (first on the buggy state to confirm the test fails, then on the fixed state to confirm it passes), and if verification fails, performs error attribution to diagnose whether the root cause is a missing environment dependency or an incorrect test command, feeding this diagnosis back to the Planning Stage.

Information flows through this pipeline as follows: raw repository metadata enters → Repository Analysis produces a structured summary → Environment Setup and Test Configuration produce build and test plans → Environment Execution materializes the environment → Verification Agent validates it → diagnostic feedback loops back to Planning for retry if needed. Successfully built environments are added to the Environment Pool for future reuse.

3.3 Roadmap for the Deep Dive

First, the formal problem formulation, which defines what "environment construction" means in mathematical terms — the triplet $(B, \mathcal{P}, T)$ , the state transition function $\delta$ , and the Fail-to-Pass (F2P) correctness criterion. This establishes the objective that the multi-agent system is trying to achieve.
Second, the Environment Reuse Mechanism in full detail — the retrieval strategy, the EnvPatchAgent's operation within a verification-driven feedback loop, and the optimization problem that motivates choosing one historical environment over another. This is the paper's most novel component and the primary source of efficiency gains.
Third, the multi-agent Planning-Execution-Verification architecture — the specific responsibilities, inputs, and outputs of each agent, how the feedback loop operates across iterations, and how the system autonomously resolves construction failures without human intervention.
Fourth, the algorithmic workflow that ties everything together, showing the decision logic for when to attempt reuse versus when to fall back to scratch construction, and how diagnostic information propagates between agents.
Fifth, a concrete case study illustrating the Environment Reuse Mechanism in action on a real repository, demonstrating the incremental patching process with actual commands.

3.4 Detailed, Sentence-Based Technical Breakdown

This is primarily a systems and infrastructure paper whose core idea is that automated environment construction for polyglot software engineering can be made both reliable and efficient by combining (1) a multi-agent architecture where specialized agents iteratively diagnose and resolve build failures, and (2) an environment reuse mechanism that leverages the incremental nature of software evolution to avoid redundant full rebuilds.

Formal Problem Definition

The paper defines environment construction as the problem of finding a configuration triplet that makes a repository's test suite executable and produces the correct differential test outcome. The formalism serves two purposes: it defines the success criteria that the multi-agent system optimizes toward, and it provides the mathematical basis for the reuse mechanism's optimization objective.

The configuration triplet. A verifiable environment is formally defined by three components:

$B \in \mathcal{S}$ — the base image, which is a pre-configured Docker image (e.g., python:3.10, ubuntu:22.04) reachable from the empty state $S_\emptyset$ via a predefined command sequence $C_B$ , such that $B = \delta(S_\emptyset, C_B)$ . The base image provides the operating system and core toolchain before any project-specific dependencies are added.
$\mathcal{P} \in \mathcal{C}$ — the build process, which is a sequence of installation commands (e.g., apt-get install, pip install, cmake, make) that transform the base image into the final environment state. The final environment state is $S = \delta(B, \mathcal{P})$ , where $\delta: \mathcal{S} \times \mathcal{C} \rightarrow \mathcal{S}$ is the state transition function that maps a starting state and a command sequence to a resulting state. Each command in $\mathcal{P}$ modifies the filesystem, installed packages, environment variables, and other system state.
$T$ — the test configuration, which specifies both how to apply the test patch (the new test cases extracted from the pull request) and which test command to execute. Unlike prior work that assumed fixed test commands (e.g., always running pytest), $T$ is synthesized by the Test Configuration Agent to match the specific repository's testing conventions.

The environment state $S$ represents a comprehensive snapshot of the computer system encompassing "all variables, files, installed packages, and system caches" (Appendix B.1). The command sequence $\mathcal{C}$ is drawn from the set of all possible shell command sequences. The state transition function $\delta$ is treated as deterministic — executing the same commands from the same starting state always produces the same resulting state.

The executability condition. The fundamental goal is that the constructed environment must allow the fixed repository state $R_{fix}$ to pass the tests:

$\varepsilon(R_{fix}, S, T) = 0$

where $\varepsilon$ is a Boolean verification function defined as:

$\varepsilon(R, S, T) = \begin{cases} 0 & \text{if all tests defined in } T \text{ pass in state } S \\ 1 & \text{otherwise} \end{cases}$

$R_{fix}$ denotes the repository state after applying the fix patch (the code changes that resolve the issue) to the base repository snapshot $R$ . The value 0 conventionally means "success" (no errors) and 1 means "failure" (at least one test failed or the test suite could not run).

What this computes: the verification function $\varepsilon$ executes the test command specified in $T$ inside the environment $S$ with the repository at state $R$ (or $R_{fix}$ ). If every test passes — meaning the test process exits with code 0 — the function returns 0. If any test fails, or if the test suite cannot be executed at all (e.g., because a required library is missing and the test runner crashes before running any tests), the function returns 1.

Why this form: a binary success/failure signal is the standard for execution-based verification in software engineering. It provides an objective, unambiguous correctness signal — unlike static analysis or human judgment, there is no ambiguity about whether the tests passed. This binary signal is also what makes the environment suitable for downstream training paradigms like RLVR, where the agent receives a clean reward of 1 for passing tests and 0 otherwise.

The Fail-to-Pass (F2P) validity criterion. Executability alone is insufficient. An environment that always passes tests regardless of the code state (e.g., because the test suite is empty or the test configuration is wrong) would satisfy Equation 1 but would be useless as a verifiable task instance. The paper therefore enforces the stricter F2P criterion:

$\varepsilon(R, S, T) = 1 \quad \land \quad \varepsilon(R_{fix}, S, T) = 0$

What this computes: the F2P criterion requires two separate test executions. First, the test suite is run on the buggy repository state $R$ (before the fix is applied), and it must fail — confirming that the environment correctly reproduces the reported issue. Second, the test suite is run on the fixed repository state $R_{fix}$ , and it must pass — confirming that the fix patch actually resolves the issue. Both conditions must hold simultaneously.

Why this form: the F2P criterion is adapted from the standard SWE-bench evaluation protocol. It ensures that the constructed environment is not merely runnable but diagnostic — it distinguishes between the buggy and fixed states. An environment that passes on both states (F2P violation because $\varepsilon(R, S, T) = 0$ ) indicates that the test patch is not actually testing the bug; an environment that fails on both states (F2P violation because $\varepsilon(R_{fix}, S, T) = 1$ ) indicates that the fix patch is incomplete or the environment is misconfigured. The conjunction $\land$ enforces both properties, and violation of either makes the environment invalid for verifiable SWE purposes.

The overall objective. The environment construction task is to find the triplet $(B, \mathcal{P}, T)$ such that $\varepsilon(R_{fix}, \delta(B, \mathcal{P}), T) = 0$ — that is, find a base image, a build command sequence, and a test configuration that together produce an environment where the fixed repository passes all tests. The F2P criterion (Equation 2) is then applied as a post-hoc validity check on the successfully built environment.

Environment Reuse Mechanism

The Environment Reuse Mechanism is MEnvAgent's primary efficiency innovation. It reformulates environment construction from "build everything from a clean base image" to "find the closest historical environment and apply minimal changes." This section begins with the formal optimization problem, then details the retrieval strategy and the verification-driven adaptation loop.

The formal optimization problem. The paper defines the reuse problem as finding a historical environment $S_{sim}$ from a pool $\mathcal{S}_{pool}$ that minimizes the expected adaptation cost:

$S_{sim} = \arg\min_{S \in \mathcal{S}_{pool}} \mathcal{C}_{adapt}(S, R)$

where $\mathcal{S}_{pool}$ is the set of all previously verified environments, $R$ is the target repository snapshot, and $\mathcal{C}_{adapt}$ is the adaptation cost — a conceptual function representing the computational effort required to transform environment $S$ into one that works for repository snapshot $R$ .

What this computes: the $\arg\min$ operator selects the single environment from the pool that minimizes the adaptation cost. In practice, $\mathcal{C}_{adapt}$ is not computed directly; instead, the paper approximates the optimal choice through a hierarchical retrieval strategy (described below) that uses software evolution heuristics as proxies for low adaptation cost.

Why this form: the optimization framing makes explicit that reuse is not always beneficial. If the adaptation cost exceeds the cost of building from scratch (which is approximately the cost of executing $\mathcal{P}$ from a base image), then reuse should not be attempted. By casting it as a minimization problem, the paper establishes that the goal is to find environments where the delta between the historical state and the target state is small — which, due to the incremental nature of software development, is typically the case for environments from the same repository at nearby versions.

The incremental patching objective. Once $S_{sim}$ is retrieved, the EnvPatchAgent generates an incremental command sequence $\Delta\mathcal{P}$ that adapts this environment to the target repository snapshot $R$ . Formally:

$\Delta\mathcal{P} = \operatorname{EnvPatchAgent}(R, S_{sim})$

such that the resulting environment $S_{new} = \delta(S_{sim}, \Delta\mathcal{P})$ satisfies the F2P criterion:

$\varepsilon(R, S_{new}, T) = 1 \quad \land \quad \varepsilon(R_{fix}, S_{new}, T) = 0$

What this computes: the EnvPatchAgent takes the target repository snapshot and the retrieved historical environment as inputs, and outputs a sequence of shell commands $\Delta\mathcal{P}$ (e.g., "checkout the repository at commit X, install the new dependency Y, update the configuration file Z"). Executing $\Delta\mathcal{P}$ against $S_{sim}$ produces $S_{new}$ , which must pass the same F2P validation as a scratch-built environment. If $S_{sim}$ already works without modification — that is, the retrieved environment already passes the tests for the target snapshot — then $\Delta\mathcal{P}$ is conceptually the empty sequence and the environment is reused directly.

Why this form: the incremental patching formulation captures the key insight that most of the environment is shared between versions of the same repository. The base operating system, system libraries, language runtimes, and the majority of project dependencies remain constant; only the specific versions of a few packages or the repository code itself need to change. By generating only the delta, the system avoids re-executing the expensive full build process $\mathcal{P}$ (which might involve recompiling large C++ codebases or re-downloading hundreds of megabytes of dependencies). The EnvPatchAgent is implemented as an LLM-based agent, not a deterministic diff tool, because the adaptation may require non-trivial reasoning — understanding that a test failure is due to a missing Python package that was added between versions, not a test configuration error.

The retrieval strategy. To approximate the optimal $S_{sim}$ , the paper employs a hierarchical retrieval strategy grounded in two software evolution principles:

Version Consistency. The system first constructs a candidate set containing only historical environments associated with the exact version of the target repository snapshot. Two snapshots are considered the same version if they correspond to the same release tag or the same commit hash. If such an environment exists in the pool (because a previous task on the same repository at the same version was already built), it is the ideal candidate — the adaptation cost is zero or near-zero because the environment was literally built for this snapshot. If no exact version match is found, the candidate set is broadened to include all historical environments belonging to the same repository, regardless of version.
Backward Compatibility. From the candidate set, the system selects the environment that is newer than the target repository snapshot yet temporally closest to it. This heuristic is "premised on the observation that newer environments typically support older dependencies" (Section 3.2). The intuition is that software evolves forward: a Docker environment built for version 2.0 of a repository likely includes all the dependencies needed for version 1.5, because dependencies accumulate over time (new packages are added, old ones are rarely removed). However, an environment built for version 1.0 might not include dependencies added in version 1.5. By selecting the chronologically closest newer environment, the system minimizes the risk of missing dependencies while also minimizing the version gap (and thus the likely adaptation effort).

What happens in practice: consider a repository with environments in the pool for versions 1.0, 1.3, and 2.1, and a new task targeting version 1.5. Version Consistency finds no exact match (1.5 is not in the pool), so the system falls back to all same-repository environments (1.0, 1.3, 2.1). Backward Compatibility selects 2.1 — it is newer than 1.5, and among the newer environments (only 2.1), it is the chronologically closest. The alternative of selecting 1.3 (closest in absolute version distance but older) would risk missing dependencies added between 1.3 and 1.5. If no newer environment exists in the pool, the system falls back to the newest available environment overall.

The verification-driven adaptation loop. Once $S_{sim}$ is retrieved, the EnvPatchAgent operates within a feedback loop rather than generating $\Delta\mathcal{P}$ in a single shot. The process proceeds as follows:

The Test Configuration Agent synthesizes the test script $T$ for the target repository snapshot $R$ . This happens regardless of whether the environment will be reused or built from scratch — $T$ is always needed.
The Verification Agent executes $T$ within $S_{sim}$ (the retrieved environment, without any patching). If the tests pass — meaning $\varepsilon(R_{fix}, S_{sim}, T) = 0$ — the environment is reused directly. No patching is needed; the historical environment already works for the target snapshot.
If verification fails, the EnvPatchAgent receives the diagnostic feedback from the Verification Agent. This feedback includes the specific test failure messages, error logs, and stack traces. The EnvPatchAgent analyzes this feedback to understand why the environment is insufficient — for example, "ImportError: No module named 'requests'" indicates a missing Python package; "cmake: command not found" indicates a missing system tool.
The EnvPatchAgent synthesizes a sequence of incremental commands $\Delta\mathcal{P}$ designed to address the identified failures. These commands are executed against $S_{sim}$ to produce an updated state $S_{new} = \delta(S_{sim}, \Delta\mathcal{P})$ .
The Verification Agent re-runs $T$ in $S_{new}$ . If the tests now pass, the process terminates successfully and $S_{new}$ is added to the Environment Pool. If verification still fails, the new diagnostic feedback is fed back to the EnvPatchAgent for another iteration. This loop continues until either the F2P criterion is satisfied or a maximum retry limit is reached (at which point the system falls back to Phase 2: scratch construction).

Why this feedback loop matters: the key risk of environment reuse is that $S_{sim}$ is almost correct but has subtle incompatibilities — a package at the wrong version, a missing configuration file, a stale compiled artifact. A single-shot patch generation would require the EnvPatchAgent to perfectly anticipate all incompatibilities from the repository metadata alone, which is unrealistic. The feedback loop allows the agent to iteratively refine its understanding: the first patch attempt might fix the most obvious error (installing a missing package), which then reveals a second error (a version conflict with an already-installed package), which requires a second patch iteration. This mirrors the iterative construction loop in Phase 2 but operates on a much smaller scale — patching an existing environment rather than building from a base image.

The concrete case study from Appendix C.2. The paper provides a detailed execution trace for the home-assistant/core repository. The system retrieves a historical environment $S_{sim}$ that was built for an earlier version of Home Assistant. When the Verification Agent runs the test script $T$ for the target snapshot, it fails with an error indicating a missing Python dependency (the specific error is a Python ImportError for a module that was added between the historical version and the target version). The EnvPatchAgent analyzes this failure, examines the repository's requirements.txt (or equivalent dependency specification) at the target snapshot, identifies that the missing module is listed as a new dependency, and generates $\Delta\mathcal{P}$ consisting of a single pip install command for that module. Executing this patch and re-running the tests succeeds, completing the reuse pathway in a fraction of the time that a full rebuild would require.

Multi-Agent Architecture: Planning-Execution-Verification Loop

When the Environment Reuse Mechanism fails (no similar environment exists, or adaptation cannot achieve F2P), the system falls back to iterative scratch construction. This section details the three stages of the loop and the responsibilities of the five specialized agents.

The overall loop structure (Algorithm 1). The construction loop runs for up to MaxRetries iterations. In each iteration, all three stages execute sequentially: Planning produces a blueprint, Execution materializes it, and Verification validates the result. If Verification fails, the diagnostic feedback is propagated back to Planning for the next iteration. If Execution fails (the installation script cannot complete), the feedback goes directly to Planning without reaching Verification. The loop terminates when Verification succeeds (the constructed environment is added to $\mathcal{S}_{pool}$ ) or when MaxRetries is exhausted (the task is recorded as a failure).

Stage 1: Planning. Three specialized agents collaborate to produce the environment blueprint:

Repository Analysis Agent. This agent receives the target repository snapshot $R$ as input — specifically, it has access to the repository's file structure (directory tree), key configuration files (e.g., requirements.txt, pom.xml, CMakeLists.txt, go.mod, package.json), and README or documentation files that describe build instructions. Its output is a structured summary containing: the identified programming language(s), the build system and package manager (e.g., pip + setuptools, Maven, Go modules, npm), the dependency requirements (both explicit declared dependencies and implicit system-level requirements inferred from the codebase), and the project's entry points (which directories contain the main source code and test code). This agent does not generate any commands; it only analyzes and summarizes.

The summary is passed to both downstream Planning agents. The inclusion of this separate analysis agent — rather than having the Environment Setup Agent directly read the repository — is a deliberate design choice: by decoupling analysis from command generation, the system allows the analysis to be reused across multiple planning iterations. If the Environment Setup Agent's first attempt fails, the Repository Analysis Agent's summary remains valid and can be fed to a second planning attempt with the diagnostic feedback, avoiding redundant repository exploration.
Environment Setup Agent. This agent consumes the repository summary and any diagnostic feedback from previous failed iterations. Its output is the base image selection $B$ and the complete build process $\mathcal{P}$ — a sequence of shell commands that, when executed starting from $B$ , will produce an environment where the repository can be built and its dependencies are satisfied. The agent must reason about: which base image provides the necessary language runtime and system libraries (e.g., python:3.10-slim vs. ubuntu:22.04 with manual Python installation), how to resolve implicit system-level dependencies that are not declared in the repository's package manager files (e.g., a Python package that requires libxml2-dev to be installed via apt-get before pip install will succeed), and the correct order of commands (system packages before language packages, compilation before installation).

The Environment Setup Agent receives diagnostic feedback from the Verification Agent via the Feedback variable in Algorithm 1. This feedback takes two forms, depending on where the failure occurred:
- If the Environment Execution Agent failed during Stage 2, the feedback consists of terminal error logs (e.g., "E: Unable to locate package libboost-all-dev", "error: command 'gcc' failed with exit status 1").
- If the Verification Agent failed during Stage 3, the feedback includes the Verification Agent's error attribution — a diagnosis of whether the test failure is due to a missing environment dependency or an incorrect test command (see Stage 3 below). If attributed to a missing dependency, the feedback specifies which dependency appears to be missing and why.
The number of retries (MaxRetries) is set to 3 per task (inferred from the algorithm structure and the global timeout of 3 hours per task from Appendix E). Each retry regenerates the complete $\mathcal{P}$ — the system does not attempt to incrementally patch a failed build script, but rather produces a new plan informed by what went wrong.
Test Configuration Agent. This agent consumes the repository summary, the proposed installation script $\mathcal{P}$ (from the Environment Setup Agent), and any diagnostic feedback. Its output is the test configuration $T$ , which includes: how to apply the test patch (which files to modify and in what order relative to the build process), the test command to execute (e.g., pytest tests/ -x, mvn test -pl module-name, go test ./...), and any environment variables or working directory settings required for the test command to function correctly.

The Test Configuration Agent must coordinate with the Environment Setup Agent's output because the test command depends on the environment setup. For example, if the installation script creates a Python virtual environment at a specific path, the test command must activate that virtual environment first. If the installation compiles the project into a build/ directory, the test command must run from the correct working directory. The agent synthesizes $T$ as a self-contained script that can be executed independently within the constructed environment $S$ .

Like the Environment Setup Agent, the Test Configuration Agent receives diagnostic feedback from failed Verification iterations. If the Verification Agent diagnoses that a test failure is due to an incorrect test command rather than a missing dependency (e.g., the test runner cannot find the test files because the working directory is wrong), this feedback goes to the Test Configuration Agent in the next iteration.

Stage 2: Execution. A single agent handles the materialization of the plan:

Environment Execution Agent. This agent receives the selected base image $B$ and the build process $\mathcal{P}$ . It instantiates a Docker container from $B$ and executes each command in $\mathcal{P}$ sequentially. Crucially, this agent is not a simple shell script runner — it monitors the terminal output in real-time and can dynamically adjust commands to resolve immediate execution errors.

The "dynamic adjustment" capability is described in Section 3.1: "capable of dynamically adjusting commands to resolve immediate execution errors (e.g., missing packages or version conflicts)." For example, if a pip install -r requirements.txt command fails because one package requires a newer version of a dependency that conflicts with another package, the agent might attempt to install the conflicting packages individually with version pins, or add a --upgrade flag. If an apt-get install command fails because a package has been renamed in the repository, the agent might search for the correct package name.

However, this dynamic adjustment capability is bounded. The agent makes "multiple attempts" (Section 3.1) to resolve installation errors within the same execution stage, but if it cannot resolve the failure after these attempts, it aborts the current execution and does not proceed to Verification. The execution status (Success or Failure) and the execution logs are returned. On failure, the execution logs become the Feedback for the next Planning iteration — the Environment Setup Agent receives the specific error messages and must generate a new $\mathcal{P}$ that avoids the issue.

If installation completes successfully, the resulting environment state $S$ (the running Docker container with all commands executed) is passed to the Verification Stage. The paper does not specify the exact number of "multiple attempts" within the execution stage, but based on the overall retry budget of 3 iterations for the full loop, it is likely 2-3 adjustment attempts per execution.

Stage 3: Verification. A single agent validates the constructed environment:

Verification Agent. This agent receives the constructed environment $S$ and the test configuration $T$ . It executes the tests defined in $T$ within the container $S$ , applying the fix patch to produce $R_{fix}$ before running the test command. The paper specifies in Section 3.1 that the verification first checks the executability condition $\varepsilon(R_{fix}, S, T) = 0$ — that is, it runs the tests on the fixed state and checks that they pass.

If the tests pass, the task is considered successful for the executability goal. The environment $S$ is added to $\mathcal{S}_{pool}$ for future reuse. Separately, the full F2P criterion (Equation 2) is verified by also running the tests on the buggy state $R$ and confirming failure. If the F2P check fails (the buggy state also passes the tests), the environment is valid in the sense of being runnable but is not a valid verifiable SWE instance — it would be discarded from the training dataset, though the paper does not explicitly discuss this edge case.

If the tests fail on $R_{fix}$ (the executability condition is not met), the Verification Agent performs error attribution — a diagnostic step that classifies whether the failure stems from (a) a missing environment dependency, or (b) an incorrect test command. This classification is critical because it determines which Planning agent receives the feedback in the next iteration. If the failure is attributed to a missing dependency (e.g., an ImportError for a Python module that was supposed to be installed by $\mathcal{P}$ ), the diagnostic feedback is directed to the Environment Setup Agent, which must modify $\mathcal{P}$ to include the missing dependency. If the failure is attributed to an incorrect test command (e.g., a FileNotFoundError because the test runner is invoked from the wrong directory), the feedback goes to the Test Configuration Agent, which must modify $T$ .

The error attribution is performed by the Verification Agent itself, which is an LLM-based agent that analyzes the test failure output and classifies the root cause. The paper does not specify the exact classification logic, but it likely involves pattern matching against common error types (import errors, compilation errors, file-not-found errors, assertion errors) and reasoning about whether the error indicates a missing software component or a misconfiguration of the test invocation.

The diagnostic feedback is propagated back to the Planning Stage as the Feedback variable in Algorithm 1, closing the loop. In the next iteration, both the Environment Setup Agent and the Test Configuration Agent receive this feedback when generating their respective outputs, ensuring that the revised plan addresses the specific failure identified in the previous attempt.

Why this architecture over simpler alternatives? A single-agent approach (like SWE-Bench-Live's interactive bash session) would require one LLM to simultaneously handle repository analysis, dependency resolution, build script generation, test configuration, execution monitoring, and failure diagnosis. The paper's decomposition into specialized agents allows each agent to have a focused prompt and a specific output format, reducing the cognitive load on the LLM and enabling more reliable performance on each subtask. The closed-loop design — where verification failures feed back to planning — is essential because environment construction is inherently trial-and-error: even an expert human cannot predict all dependency conflicts in advance. The separation of Environment Setup from Test Configuration is particularly important because these two tasks require different expertise: the former is about system administration and package management, while the latter is about understanding the repository's testing conventions and test framework.

Complete Algorithmic Workflow

The full MEnvAgent workflow is specified in Algorithm 1 (Appendix C.1). This section walks through the decision logic and information flow.

Phase 1: Environment Reuse (lines 2-16). The system first calls RetrieveSimilarEnv to query $\mathcal{S}_{pool}$ using the retrieval strategy described above. This function returns either a historical environment $S_{sim}$ or Null if no suitable candidate exists (for example, if this is the first task from a repository, the pool contains no environments for that repository at all).

If $S_{sim}$ is found, the Test Configuration Agent synthesizes $T$ for the target repository. The Verification Agent then runs $T$ against $S_{sim}$ without any patching. If verification succeeds, $S_{sim}$ is returned immediately — this is the "direct reuse" case, which incurs only the cost of running the tests.

If verification fails, the system enters the patching sub-loop (lines 9-14). The EnvPatchAgent generates $\Delta\mathcal{P}$ based on the target repository, the retrieved environment, and the verification logs. $\Delta\mathcal{P}$ is executed against $S_{sim}$ to produce $S_{new}$ , and the Verification Agent tests $S_{new}$ . If this succeeds, $S_{new}$ is returned. Note that the patching sub-loop in Algorithm 1 shows only a single attempt — if patching fails, the system falls through to Phase 2. The paper does not explicitly state whether multiple patching iterations are attempted within Phase 1 (the text in Section 3.2 describes an "iterative process" for the EnvPatchAgent, suggesting multiple attempts are possible), but Algorithm 1 shows a single shot before falling back.

Phase 2: Iterative Construction (lines 18-39). The Feedback variable is initialized to empty. The loop runs for up to MaxRetries iterations (3, based on the retry budget):

Planning sub-stage (lines 22-24). The Repository Analysis Agent produces Summary from $R$ . The Environment Setup Agent produces $\mathcal{P}$ and $B$ from Summary and Feedback. The Test Configuration Agent produces $T$ from Summary, $\mathcal{P}$ , and Feedback. In the first iteration, Feedback is empty, so agents generate their plans based only on repository analysis. In subsequent iterations, Feedback contains the diagnostic information from whatever failed in the previous iteration.
Execution sub-stage (lines 26-30). The Environment Execution Agent takes $B$ and $\mathcal{P}$ , instantiates a container, and executes the commands. It returns the environment state $S$ , a status (Success or Failure), and the execution logs. If the status is Failure, the execution logs become the new Feedback, and the loop continues to the next iteration (skipping Verification, since there is no environment to verify).
Verification sub-stage (lines 32-38). The Verification Agent runs $T$ in $S$ . It returns a boolean Verified (True if tests pass, False otherwise) and a Diagnosis (the error attribution). If Verified is True, $S$ is added to $\mathcal{S}_{pool}$ and returned as the successful result. If Verified is False, Diagnosis becomes the new Feedback, and the loop continues.

If the loop exhausts MaxRetries without success, the algorithm returns Failure for this task.

Why this two-phase structure? Phase 1 (Reuse) is attempted first because it is dramatically cheaper — patching an existing environment typically involves executing a handful of commands rather than a full build process. Only when reuse is impossible or fails does the system incur the cost of Phase 2. This is a form of speculative execution: the system bets that a similar environment exists and can be cheaply adapted, and only pays the full cost when that bet fails. As the Environment Pool grows (more repositories and more versions), the probability of Phase 1 succeeding increases, creating a virtuous cycle where the system becomes more efficient over time.

Agent Specifications and Implementation Details

Table 5 in Appendix C.1 provides the formal Input-Output specifications for each agent. These are summarized here with additional context:

Repository Analysis Agent.

Input: the target repository $R$ — specifically, access to the repository's file structure at the target commit, including all source files, configuration files, and documentation.
Output: a structured summary containing the project type (e.g., "Python web application using Flask"), the build system and package manager, the dependency requirements (both explicit and implicit), and the entry points for source code and tests.
Why this specification: the structured format ensures that downstream agents receive consistent, machine-parseable information regardless of the repository's language or complexity. The requirement to identify both explicit and implicit dependencies forces the agent to reason beyond simply reading a requirements.txt — it must infer, for example, that a Python package using C extensions will need python3-dev and a C compiler.

Environment Setup Agent.

Input: the repository summary (from Repository Analysis Agent) and the diagnostic feedback (from previous failed iterations, if any).
Output: the base image selection $B$ (a specific Docker image tag) and the build process $\mathcal{P}$ (an ordered sequence of shell commands).
Why this specification: separating base image selection from the build commands allows the agent to reason about tradeoffs — a larger base image (e.g., python:3.10 rather than python:3.10-slim) might include pre-installed system libraries that eliminate the need for apt-get commands, at the cost of a larger image size and longer download time.

Test Configuration Agent.

Input: the repository summary, the proposed installation script $\mathcal{P}$ , and the diagnostic feedback (if any).
Output: the test configuration $T$ , including the test patch application instructions and the test execution command with any required environment variables or working directory settings.
Why this specification: receiving $\mathcal{P}$ as input allows the Test Configuration Agent to coordinate with the environment setup. If $\mathcal{P}$ creates a Python virtual environment at /venv, the test configuration must include source /venv/bin/activate before running pytest. Without this coordination, the test command might fail even though the environment is correctly built.

Environment Execution Agent.

Input: the base image $B$ and the build process $\mathcal{P}$ .
Output: the environment state $S$ (a running Docker container), an execution status (Success/Failure), and execution logs.
Why this specification: returning both the status and the logs ensures that downstream components can distinguish between "installation succeeded" (proceed to verification) and "installation failed" (logs become feedback for planning). The environment state $S$ is passed by reference (the container ID) rather than by value (a complete filesystem snapshot).

EnvPatchAgent (for Environment Reuse Mechanism).

Input: the target repository $R$ , the retrieved environment $S_{sim}$ , and the verification logs from the failed test execution.
Output: the incremental command sequence $\Delta\mathcal{P}$ .
Why this specification: receiving the verification logs allows the agent to target its patching at the specific failures observed. Without these logs, the agent would have to guess what needs to change — a much harder problem.

Verification Agent.

Input: the environment state $S$ and the test configuration $T$ .
Output: a boolean Verified (True if tests pass) and a Diagnosis (error attribution if tests fail).
Why this specification: the Diagnosis output is what enables the feedback loop. A boolean pass/fail alone would not tell the Planning agents what to change; the error attribution provides actionable guidance.

Hyperparameters and configuration (from Appendix E, Table 8). All experiments use a fixed temperature of 0.5 for LLM generation (balancing diversity for exploration with consistency for reliable command generation) and a global timeout of 3 hours (10,800 seconds) per task. The MaxRetries for the iterative construction loop is 3, inferred from the retry budget and the structure of Algorithm 1. The Environment Pool $\mathcal{S}_{pool}$ is populated as successful environments are built — the paper does not specify a maximum pool size or an eviction policy, suggesting that all successfully built environments are retained indefinitely.

LLM backbones. The agents are powered by one of two LLMs, chosen to assess robustness: Kimi-K2 (kimi-k2-0905-preview), an open-source model selected for "superior capability in agentic planning and long-context understanding," and Gemini-3-Flash, a closed-source model representing "the latest state-of-the-art capabilities while maintaining low latency and high cost-efficiency" (Section 5, Model Details). All agents within a single run share the same backbone model — the system does not use different models for different agents. The choice of these two specific models reflects a deliberate strategy: one open-source (enabling reproducibility and community adoption) and one closed-source (establishing an upper bound on what the best available models can achieve).

Failure handling and recovery. The system has three levels of error recovery, corresponding to increasingly expensive fallbacks:

Within-execution adjustment (cheapest): the Environment Execution Agent dynamically modifies commands when it encounters errors, without triggering a full planning retry. This handles simple issues like package name typos or missing version pins.
Planning retry (moderate cost): if within-execution adjustment fails, or if verification fails, the entire plan is regenerated with diagnostic feedback. This requires re-executing the Planning Stage and re-running the (potentially modified) build process.
Scratch construction fallback (most expensive): if the Environment Reuse Mechanism fails, the system builds from a base image. This is the standard construction pathway and is only invoked when reuse is impossible.
Task failure (terminal): if MaxRetries scratch construction attempts all fail, the task is abandoned. The paper reports task-level success rates (Pass Rate and F2P Rate) that aggregate across both reuse and scratch pathways.

Design Choices and Their Justifications

Why a multi-agent architecture over a monolithic agent? The paper argues implicitly that environment construction requires diverse expertise — understanding repository structure, resolving system-level dependencies, configuring language-specific build tools, and diagnosing test failures — that is difficult for a single LLM prompt to handle reliably. By decomposing the task across specialized agents, each with a focused responsibility and a specific output format, the system reduces the cognitive load per agent and enables more targeted error recovery. When a test fails because of a misconfigured test command, only the Test Configuration Agent needs to revise its output; the Environment Setup Agent's output remains valid. A monolithic agent would need to regenerate everything, increasing both cost and the risk of introducing new errors.

Why a Planning-Execution-Verification loop over single-shot generation? Environment construction is fundamentally a trial-and-error process. Even expert human developers rarely write a correct Dockerfile for a complex legacy project on the first attempt; they iterate, run the build, observe failures, and adjust. The loop structure mirrors this human workflow: generate a hypothesis (Planning), test it empirically (Execution), observe the results (Verification), and refine (next Planning iteration). A single-shot approach would require the LLM to perfectly anticipate all dependency conflicts, version incompatibilities, and platform-specific issues before any empirical feedback — an unrealistic requirement for repositories that may not have been built in years.

Why the Environment Reuse Mechanism over always building from scratch? This is an efficiency argument rooted in software evolution patterns. Most software changes are incremental: a new version of a repository typically adds a few dependencies, modifies some source files, and updates some configuration, but leaves the vast majority of the environment unchanged. Rebuilding from scratch for every version discards all prior work and re-executes hundreds of commands that would produce identical results. The reuse mechanism exploits this incremental property to achieve 43% time cost reduction (Table 2) while actually improving success rates (by 18.5% compared to the no-reuse baseline, per the ablation in Table 3) because patching an already-working environment avoids the risk of introducing new errors during a full rebuild.

Why the hierarchical retrieval strategy (Version Consistency → Backward Compatibility)? The retrieval strategy encodes two software engineering heuristics as a priority order. Version Consistency is highest priority because an exact-version match implies zero adaptation cost — the environment was literally built for this snapshot. Backward Compatibility is second priority because it leverages the monotonic nature of dependency accumulation: newer environments are supersets of older ones, so adapting backward (making a newer environment work for an older snapshot) involves removing or downgrading things, which is generally easier than adding missing components to an older environment. This ordering is a design choice informed by domain knowledge, not learned from data.

Why a dedicated EnvPatchAgent over a simple diff-based patch? The adaptation from $S_{sim}$ to the target snapshot is not always reducible to a deterministic diff of configuration files. The EnvPatchAgent must reason about why a test failed in the retrieved environment — is the failure due to a missing package, a version mismatch, a stale compiled artifact, or an environmental difference (e.g., a different operating system version)? A diff-based approach would only detect changes in version-controlled files; it would miss, for example, that the retrieved environment has Python 3.10 but the target snapshot requires a feature introduced in Python 3.11. The EnvPatchAgent, being LLM-based, can interpret error messages and infer the root cause.

Why the Fail-to-Pass (F2P) criterion as the validity check? A pass-only criterion ( $\varepsilon(R_{fix}, S, T) = 0$ ) is insufficient because it does not verify that the test actually tests the bug. A trivial environment where the test suite is empty or the test command always succeeds would satisfy pass-only but would be useless as a verifiable task. The F2P criterion ensures that the environment reproduces the bug (the test fails on the buggy state) and verifies the fix (the test passes on the fixed state). This is adapted directly from the SWE-bench evaluation protocol and has become the standard for verifiable SWE benchmarks.

4. Key Insights and Innovations

Innovation 1: Environment Construction as a Reuse Problem Rather Than a Build-From-Scratch Problem

The paper's most conceptually distinctive move is reframing environment construction — which the field had implicitly treated as an independent build problem for each task — as a reuse-and-adapt problem. This shift in framing is what enables the 43% time reduction and the 18.5% Pass Rate improvement over the no-reuse baseline (Table 3), and it represents a fundamental insight about software evolution rather than an incremental engineering optimization.

What the dominant assumption was. Prior to MEnvAgent, every automated environment construction method — Repo2Run, SWE-Bench-Live, SWE-Factory — treated each task as a clean-slate build from a base Docker image. The field's mental model was: repository snapshot → analyze dependencies → install everything → run tests. Even SWE-Factory's more sophisticated multi-agent architecture operates within this paradigm. The assumption was that environments are fragile, that version differences make historical environments incompatible with new tasks, and that the safe approach is to rebuild every time. This is not an unreasonable assumption — Docker environments are fragile, and the "it works on my machine" problem is notorious — but it's an assumption that the paper identifies as unnecessarily expensive.

What MEnvAgent does differently at the conceptual level. The paper recognizes that software environments evolve incrementally, not independently. A Docker environment built for version 1.3 of a repository shares the overwhelming majority of its state with an environment needed for version 1.5: the same operating system, the same language runtime, the same core dependencies, the same build toolchain. Only the delta between versions — a few new packages, some updated configuration files, the changed source code — needs to be modified. Rebuilding from scratch discards all prior work and re-executes hundreds of commands that would produce identical results.

This is not a mechanism innovation (other papers have used caching and incremental builds in different contexts) — it's a framing innovation. The paper formalizes environment construction as an optimization problem over an environment pool: find the historical environment that minimizes expected adaptation cost, then synthesize the minimal delta. The entire Phase 1 of the algorithm (lines 2-16) exists because of this reframing. The Environment Pool is not an implementation detail; it's a first-class component that grows over time, making the system increasingly efficient as more tasks are processed — a property no prior system exhibits.

Evidence of the power of this framing. The ablation study in Table 3 is definitive. Removing the EnvPatchAgent (but keeping retrieval — the "w/o EnvPatchAgent" variant) causes the Reuse Success Rate to drop from 39.0% to 25.0%, and time cost increases by 20% due to frequent fallbacks to scratch builds. This isolates the contribution of the adaptation capability: retrieval alone is not enough; you need the framing that the problem is about patching a retrieved environment, not just finding the closest match. Compared to the no-reuse baseline, the full framework reduces time by 46.0% and improves Pass Rate by 18.5% — the latter being a surprising result that suggests building from scratch introduces new errors that patching an already-working environment avoids. The data scale analysis in Figure 4 further validates the reframing: as the number of instances per repository grows from 1 to 10, the Reuse Success Rate rises from near-zero to 39%, demonstrating that the value of reuse compounds with scale — exactly what you'd expect if the incremental-evolution hypothesis is correct.

Significance beyond performance. This reframing makes MEnvAgent self-improving over time. Each successfully built environment becomes a candidate for future reuse, so the system's efficiency increases with cumulative usage. This is a qualitatively different property from prior systems, which have fixed efficiency regardless of how many environments they've built. For organizations running large-scale batch inference or maintaining continuously updated benchmarks, this compounding efficiency gain could make the difference between feasibility and infeasibility at scale. It also connects to broader infrastructure patterns (like Docker layer caching) but applies them at a semantic, LLM-driven level rather than a filesystem-hash level — the EnvPatchAgent reasons about why an environment needs to change, not just which files are different.

Innovation 2: Error Attribution as the Bridge Between Verification and Regeneration

The paper's second conceptual contribution is the explicit separation of error attribution — diagnosing why a test failed — from the act of detecting failure, and routing that diagnosis to the appropriate specialized agent. This is a diagnostic innovation that transforms the Planning-Execution-Verification loop from a blind retry mechanism into a targeted, information-efficient recovery process.

What the dominant assumption was. Prior multi-agent systems for environment construction (principally SWE-Factory) also used iterative loops: build, test, retry. But the standard approach was to feed raw error logs back to a general planning agent and ask it to "try again with this feedback." This treats all failures uniformly — a missing dependency, a misconfigured test command, and a compilation error all produce the same "try again" response, differing only in the text of the error message that the planner must interpret. There's no architectural distinction between different failure modes; the recovery logic is entirely implicit in the LLM's reasoning.

What MEnvAgent does differently at the conceptual level. The Verification Agent doesn't just report pass/fail — it performs a classification step that attributes the failure to one of two distinct root causes: (a) a missing environment dependency (the build process $\mathcal{P}$ is incomplete), or (b) an incorrect test command (the test configuration $T$ is wrong). This classification determines which Planning agent receives the feedback in the next iteration. If a dependency is missing, the Environment Setup Agent gets the diagnosis and revises $\mathcal{P}$ . If the test command is wrong, the Test Configuration Agent gets the diagnosis and revises $T$ .

This is a routing architecture, not just a feedback mechanism. It decomposes the recovery problem into two independent sub-problems, each handled by a specialist. A monolithic retry system would require the Environment Setup Agent to also infer that a test command might be wrong — or the Test Configuration Agent to infer that a dependency might be missing — creating confusion about which component to modify. By explicitly attributing the failure to one of two causes, MEnvAgent prevents unnecessary changes to working components and focuses the revision effort where it's actually needed.

Why this matters for reliability. The error distribution analysis in Figure 6 provides indirect evidence for the importance of this attribution. Across languages, the failure modes are qualitatively different: Go and Python are dominated by test execution failures (suggesting test configuration issues), while C/C++ are dominated by environment setup failures (dependency and compilation issues). Java shows a language-specific pattern where Gemini-3-Flash has half the setup failure rate of Kimi-K2, suggesting that the two models make different types of errors. Without explicit error attribution, the system would have to guess which component to fix — and getting this guess wrong would waste an entire iteration on modifying the wrong plan. With attribution, the system routes the diagnosis to the right agent deterministically.

Significance beyond raw performance. Error attribution is a diagnostic primitive that could generalize beyond environment construction. Any multi-agent system that involves generating plans and then executing them against an environment — code generation with test execution, infrastructure-as-code with validation, scientific workflow construction — faces the same challenge: when execution fails, which part of the plan was wrong? The paper's explicit decomposition of failure modes and routing of diagnoses to specialized agents is a design pattern, not just a performance optimization. It's incremental in the sense that it builds on the standard Planning-Execution-Verification loop, but fundamental in the sense that it introduces a classification layer between detection and recovery that changes the nature of the feedback loop from implicit (the LLM must figure out what went wrong) to explicit (the architecture tells you which component to fix).

Innovation 3: The F2P Criterion as a Necessary and Sufficient Condition for Verifiable SWE Environments

While the Fail-to-Pass criterion itself originates in SWE-bench evaluation, the paper's contribution is elevating it from an evaluation metric to a construction-time validity condition — and formalizing it as a Boolean predicate that the system explicitly verifies before accepting an environment. This is a subtle but important shift from "evaluate whether an environment is good" to "construct environments that provably satisfy this property."

What the prior approach was. Prior automated environment construction tools either didn't verify F2P at all (Repo2Run "focus[es] exclusively on environment installation via fixed test commands that do not execute verification tests" — Section 7) or used executability alone as the success criterion. An environment that passes tests on the fixed state was considered successful, without checking whether it also reproduces the failure on the buggy state. This creates a subtle failure mode: an environment might be misconfigured such that the test suite always passes (e.g., the test command is wrong and doesn't actually run any tests, or the test patch wasn't properly applied), satisfying the executability condition but producing a useless verifiable task instance.

What MEnvAgent does differently at the conceptual level. The paper formalizes the environment construction objective as a two-stage verification that must both hold simultaneously: $\varepsilon(R, S, T) = 1$ (the buggy state fails) AND $\varepsilon(R_{fix}, S, T) = 0$ (the fixed state passes). This is not just an evaluation detail — it's baked into the system architecture (Section 3.1, Verification Stage: "Finally, we verify the successful environment against the F2P criterion to confirm its validity"). The system explicitly checks both conditions and rejects environments that satisfy executability but fail F2P.

This matters because it closes a semantic gap between "the environment runs" and "the environment reproduces the bug." A pass-only system can produce environments that look successful but would produce incorrect training signals for downstream RLVR pipelines — the agent would learn from environments where the "correct" fix is unnecessary because the tests pass regardless. By enforcing F2P at construction time, MEnvAgent guarantees that every environment in its output pool is genuinely diagnostic.

Evidence of the distinction's importance. The paper reports both Pass Rate (executability) and F2P Rate (validity) separately for all experiments (Table 2, Table 9). The gap between these metrics is informative: across the MEnvAgent results with Kimi-K2, the Pass Rate averages around 50-60% while F2P is around 30-40%, meaning approximately one-third of executable environments fail the F2P check. These are environments that would have been counted as successes under a pass-only criterion but are actually invalid as verifiable SWE instances. The paper doesn't explicitly analyze what fraction of the Pass Rate → F2P gap is due to the Fail condition failing (buggy state also passes) versus the Pass condition (fixed state still fails), but the existence of the gap validates that F2P enforcement is materially different from executability enforcement.

Significance. This is an incremental contribution in the sense that the F2P concept predates MEnvAgent, but it's fundamental in the sense that embedding it into the construction pipeline changes what the system optimizes for. Prior systems optimized for "make the tests pass" — which is necessary but not sufficient. MEnvAgent optimizes for "make the environment reproduce the bug and verify the fix" — which is both necessary and sufficient for the environment to be useful in verifiable SWE workflows. As the field moves toward large-scale automated dataset generation for RLVR, this distinction becomes critical: a dataset of pass-only environments would inject noise into the training signal, while a dataset of F2P-verified environments provides clean binary rewards.

Innovation 4: Complementary Strengths of Reuse and Multi-Agent Iteration Across Language Ecosystems

The paper's experimental analysis reveals a pattern that goes beyond the headline aggregate numbers: the two architectural innovations — Environment Reuse and the multi-agent Planning-Execution-Verification loop — have complementary strengths that manifest differently across programming languages, and combining them yields robustness that neither achieves alone.

What's distinctive about this finding. It would be natural to assume that the multi-agent architecture is the primary driver of success rates (it handles complexity) and the reuse mechanism is the primary driver of efficiency (it reduces time costs). The ablation study complicates this picture. Table 3 shows that removing reuse not only increases time cost by 46% but also reduces Pass Rate by 18.5%. This is a non-obvious result: why would building from scratch produce lower success rates than patching an existing environment? The most plausible explanation is that building from scratch introduces more opportunities for error — each new dependency resolution, each compilation step, each configuration choice is a potential failure point. Patching an already-working environment avoids re-solving already-solved problems, which not only saves time but also reduces the probability of introducing a new error during the rebuild.

This means the reuse mechanism is not purely an efficiency optimization — it's also a reliability mechanism. It restricts the search space for environment construction from "all possible configurations" to "configurations near a known-good state," which is a smaller and more predictable space to navigate. This is conceptually similar to how transfer learning or warm-starting reduces variance in optimization problems, but applied to the discrete, combinatorial domain of environment configuration.

The language-specific dimension. Figure 6 shows that failure modes vary dramatically across languages: C/C++ dominates in environment setup failures (compilation errors from complex CMake configurations), while Go and Python have higher proportions of test execution failures. The per-language performance breakdown (Table 9) shows that MEnvAgent's advantage over SWE-Factory is not uniform — it's larger in languages with complex build systems (Java, C++) and smaller in languages with standardized package ecosystems (Python, Go). This suggests that the multi-agent architecture's error attribution and targeted recovery are most valuable when the build process is complex and failure-prone, while the reuse mechanism provides more consistent benefits across all languages by avoiding rebuilds entirely.

Why this matters beyond MEnvAgent. The complementarity finding suggests a general principle for automated infrastructure construction: combine global search (iterative multi-agent planning, which explores the space of possible configurations) with local adaptation (reuse-and-patch, which exploits proximity to known-good states). Global search is necessary for novel configurations where no close historical example exists; local adaptation is more efficient and reliable when a close example does exist. The two-phase architecture (try reuse first, fall back to construction) implements this principle directly. This is not a novel theoretical insight — it's a standard explore-exploit tradeoff — but the paper provides empirical evidence that it applies in the specific, high-stakes domain of environment construction, where the cost of failed exploration (a broken build) is high and the benefit of successful exploitation (a 46% time savings) is substantial.

Significance. This finding is incremental in the sense that it emerges from standard ablation and analysis techniques, but it provides a causal narrative for why MEnvAgent works that goes beyond "we built a better system." The paper doesn't just report that MEnvAgent outperforms baselines — it provides evidence that the two mechanisms contribute in different ways, and that the full system benefits from their interaction. This is important for practitioners who need to decide whether to adopt the full framework or just the reuse mechanism or just the multi-agent architecture. The answer, based on this analysis, is that you need both: reuse alone (without the EnvPatchAgent's reasoning) has a 25% Reuse Success Rate, and scratch construction alone (without reuse) has lower Pass Rates and higher time costs. The synergy matters.

5. Experimental Analysis

Evaluation Methodology

Dataset. MEnvBench is a newly constructed benchmark comprising 1,000 tasks across 10 programming languages (Python, Go, Java, JavaScript, C, C++, Rust, TypeScript, PHP, Ruby). Each language contributes 100 tasks, structured as 20 repositories × 5 instances per repository, with instances selected from distinct historical versions of each repository. Tasks are drawn from 200 unique GitHub repositories spanning 2018–2025, with strict filtering criteria: repositories must have >1,000 stars, >200 forks/issues/PRs, and >60% primary language ratio, while individual instances must have closed issues, non-empty problem descriptions, test patches, and fix patches, with patch sizes ≤1,000 lines of code and ≤10 files modified. An LLM-based quality evaluator (DeepSeek-V3.2) scores issue descriptions for semantic clarity, discarding instances scoring below 5. The benchmark is further balanced across application domains (10 distinct categories including ML/AI, Database Systems, Web Applications) and project sizes (from <10MB to >500MB).
Base model(s). Two LLMs serve as the reasoning backbone for the agents: Kimi-K2 (kimi-k2-0905-preview), an open-source model selected for "superior capability in agentic planning and long-context understanding," and Gemini-3-Flash, a closed-source model representing "the latest state-of-the-art capabilities while maintaining low latency and high cost-efficiency, which are critical prerequisites for scalable environment construction scenarios" (Section 5, Model Details). All agents within a single run share the same backbone — the system does not mix models across agent roles. This dual-model design enables robustness assessment: by comparing an open-source and a closed-source model on identical tasks, the paper checks whether MEnvAgent's architecture provides benefits that generalize beyond any single model's capabilities.
Metrics. Three metrics are reported: (1) Pass Rate (PASS): the percentage of tasks where the constructed environment satisfies the executability condition — the fixed repository state $R_{fix}$ passes all tests ( $\varepsilon(R_{fix}, S, T) = 0$ ). This measures whether the environment can run the test suite successfully, regardless of whether it reproduces the bug. (2) Fail-to-Pass Rate (F2P): the percentage of tasks satisfying the full validity criterion — the buggy state $R$ fails tests AND the fixed state $R_{fix}$ passes tests ( $\varepsilon(R, S, T) = 1 \land \varepsilon(R_{fix}, S, T) = 0$ ). This is the stricter metric that determines whether an environment is genuinely useful as a verifiable SWE task instance. (3) Time Cost (TIME): the average wall-clock time consumed per task in seconds, measuring computational efficiency. The F2P vs. Time tradeoff is the primary lens for comparing methods, since higher success rates at lower time costs is the ideal operating point.
Baselines. Three categories of baselines are compared: (1) Repo2Run, a Python-specialized tool evaluated "exclusively on the Python subset due to its extensibility constraints" (Section 5, Baseline Methods); (2) SWE-Bench-Live, a system that supports 6 of the 10 MEnvBench languages, allowing a multi-language sub-evaluation; and (3) SWE-Factory, a state-of-the-art agent framework evaluated across all 10 languages, representing the strongest prior multi-agent approach. SWE-Factory is described in the paper as introducing "a collaborative multi-agent architecture for automated environment construction" (Section 7) and supporting four programming languages in its original form, though the MEnvAgent paper extends its evaluation to all 10 MEnvBench languages.
Generation budget / compute accounting. Compute is measured in wall-clock time per task, with a global timeout of 3 hours (10,800 seconds) per task applied uniformly across all methods and all models (Appendix E, Table 8). This timeout serves as the hard constraint on per-task computation. The paper also reports token consumption and estimated dollar cost per task (Table 10), calculated using the pricing of each model: Kimi-K2 at $0.6 per million input tokens and$ 2.5 per million output tokens; Gemini-3-Flash at $0.5 per million input tokens and$ 1.5 per million output tokens.
Cross-validation / statistical protocol. The paper does not employ cross-validation or statistical significance testing on MEnvBench. Results are reported as aggregate percentages across all 100 tasks per language (or the applicable subset for Repo2Run and SWE-Bench-Live). The paper notes that all experiments use a fixed temperature of 0.5 for LLM generation, and Table 8 in Appendix E specifies detailed hyperparameters for each method (including retry budgets, execution timeouts, and agent-specific settings). The paper does not report confidence intervals, standard deviations, or multiple runs with different random seeds for any metric. For the downstream fine-tuning experiments in Section 6.3, the paper uses standard train-test splits with separate evaluation benchmarks (SWE-bench Verified and SWE-bench Multilingual), ensuring no data leakage between training and evaluation.

Main Quantitative Results

Aggregate Performance Across All Languages on MEnvBench

Table 2 reports the averaged performance across all 10 languages for each method-model combination. The headline results are:

MEnvAgent with Kimi-K2: F2P Rate of 33.0%, Pass Rate of 52.0%, Time Cost of 637 seconds (≈10.6 minutes) per task. With Gemini-3-Flash, F2P Rate of 33.6%, Pass Rate of 53.2%, Time Cost of 621 seconds per task.
SWE-Factory (strongest baseline) with Kimi-K2: F2P Rate of 24.0%, Pass Rate of 41.0%, Time Cost of 1,118 seconds (≈18.6 minutes). With Gemini-3-Flash, F2P Rate of 25.5%, Pass Rate of 42.2%, Time Cost of 1,089 seconds.

Averaged across models, MEnvAgent improves the F2P Rate by 8.6 percentage points (from 24.75% to 33.3%) and the Pass Rate by 11.0 percentage points (from 41.6% to 52.6%), while reducing time costs by 43.0% (from 1,103.5 seconds to 629 seconds). These are the paper's headline performance claims, explicitly stated in the abstract and Section 5.

The scatter plot in Figure 3 operationalizes this comparison as a tradeoff analysis. The x-axis is average time cost per task; the y-axis is either F2P Rate (Figure 3a) or Pass Rate (Figure 3b). MEnvAgent points cluster in the top-left quadrant — high success rates, low time costs — for both Kimi-K2 and Gemini-3-Flash, across all languages. In contrast, SWE-Factory points "are predominantly distributed in the right-hand region," reflecting high time costs from "inefficient trial-and-error loops" (Section 5). Repo2Run and SWE-Bench-Live "cluster in the lower region" — they maintain moderate efficiency but their success rates are "significantly compromised." This visual analysis confirms that no baseline simultaneously achieves the efficiency and success rate of MEnvAgent.

Per-Language Performance Breakdown

Table 9 in Appendix F provides the comprehensive per-language breakdown. Key patterns include:

Modern languages with standardized ecosystems show the highest success rates. Python: MEnvAgent with Kimi-K2 achieves 56% F2P and 76% Pass Rate, compared to SWE-Factory's 54% F2P and 72% Pass Rate. Go: MEnvAgent achieves 54% F2P and 74% Pass Rate versus SWE-Factory's 28% F2P and 36% Pass Rate. The Go result is a standout — MEnvAgent nearly doubles SWE-Factory's F2P rate — suggesting that Go's standardized build tooling benefits from the multi-agent architecture's ability to correctly configure go mod and go test invocations, while SWE-Factory's trial-and-error approach struggles to converge on the correct test configuration.

Complex compiled languages show larger performance gaps. C++: MEnvAgent with Kimi-K2 achieves 16% F2P versus SWE-Factory's 6%; Gemini-3-Flash achieves 30% F2P versus 18%. C: Kimi-K2 achieves 12% F2P versus SWE-Factory's 4%; Gemini-3-Flash achieves 20% F2P versus 12%. The time cost advantage is also pronounced for these languages — for C++ with Kimi-K2, MEnvAgent takes 3,487 seconds versus SWE-Factory's 5,022 seconds (a 30.6% reduction), and for C with Gemini-3-Flash, 2,376 seconds versus 4,644 seconds (a 48.8% reduction). These large gaps are consistent with the hypothesis that the multi-agent architecture's error attribution and targeted recovery are most valuable when build processes are complex and error-prone.

Languages where MEnvAgent trails particular baselines on particular metrics. For Python with Kimi-K2, SWE-Factory actually has lower time cost (1,013 seconds versus MEnvAgent's 1,234 seconds), though MEnvAgent has moderately higher success rates (56% F2P versus 54%). For PHP with Kimi-K2, SWE-Factory achieves 28% F2P versus MEnvAgent's 24%, though MEnvAgent's time cost is lower (599 versus 630 seconds). For Ruby with Gemini-3-Flash, SWE-Factory achieves 34% F2P versus MEnvAgent's 32%, though MEnvAgent's time cost is substantially lower (552 versus 990 seconds). These mixed results on specific language-model combinations suggest that MEnvAgent's advantage is not universal — it arises from particular architectural features that matter more for certain languages (those with complex dependencies) and certain error patterns (those requiring the targeted attribution that MEnvAgent provides).

The single-language baselines show their limitations. Repo2Run (Python only) achieves 34% F2P with Kimi-K2 and 36% with Gemini-3-Flash, with time costs of 1,401 and 883 seconds respectively — lower success rates than MEnvAgent on the same Python subset. SWE-Bench-Live, evaluated on the 6 languages it supports, shows particularly low success rates on Go (10% F2P with Kimi-K2) and Java (6% F2P), confirming that its single-agent architecture struggles with non-Python ecosystems.

Efficiency-Cost Tradeoff Analysis

Table 10 in Appendix F reports the economic efficiency of each method. Key findings:

MEnvAgent and SWE-Factory both operate in a low-cost regime. For Kimi-K2, MEnvAgent's average cost per task ranges from $0.07 (Ruby, Rust) to$ 0.15 (C, C++), while SWE-Factory ranges from $0.05 (Ruby, PHP) to$ 0.10 (C, C++). For Gemini-3-Flash, MEnvAgent ranges from $0.18 (Rust) to$ 0.57 (C++), while SWE-Factory ranges from $0.09 (JavaScript) to$ 0.27 (C). The paper notes that "although MEnvAgent incurs a marginally higher cost than SWE-Factory, this slight increment is well-justified by the significant gains in both F2P rate and time efficiency" and that "both methods operat[e] within a highly affordable low-cost regime, [so] this difference is negligible in practice and does not constitute a bottleneck for large-scale data expansion."

Single-agent baselines incur substantially higher costs. Repo2Run (Python only) costs $0.38 per task with Kimi-K2 and$ 0.46 with Gemini-3-Flash — 3-4× higher than MEnvAgent on Python ( $0.09–$ 0.26). SWE-Bench-Live costs range from $0.46 (TypeScript) to$ 1.35 (Python) with Gemini-3-Flash — up to 5× higher than MEnvAgent on the same language-model combinations. This cost differential "is attributable to unplanned exploration" (Table 10 analysis) — single-agent systems generate longer, less focused interaction traces, consuming more tokens without commensurate success rate improvements.

Token consumption patterns reflect architectural differences. MEnvAgent's input token counts are higher than SWE-Factory's for both models (e.g., Kimi-K2 on Python: 141k input for MEnvAgent versus 90k for SWE-Factory), while output token counts are similar or lower (9k output versus 12k). This suggests that MEnvAgent spends more tokens on context (providing each specialized agent with comprehensive repository information and diagnostic feedback) but produces more concise, targeted outputs — consistent with the architecture's decomposition of the problem into focused subtasks.

Ablation Study of Environment Reuse

Experimental setup. The ablation study (Section 6.1) compares three variants: (1) MEnvAgent (Full), the complete system with both Environment Retrieval and EnvPatchAgent; (2) w/o EnvPatchAgent (Direct), which retrieves the most similar environment but applies it directly without modification — testing whether retrieval alone provides benefits without the patching capability; and (3) w/o Reuse (Scratch), which disables the reuse mechanism entirely and builds every task from the base image. All experiments use Kimi-K2 on a Python subset of MEnvBench, with the data scale extended to 10 instances per repository. The primary metric for reuse efficacy is Reuse Success Rate (RSR): the proportion of tasks successfully verified via the reuse pathway without falling back to scratch construction.

Component Effectiveness (Table 3). Results:

MEnvAgent (Full): Reuse Success Rate 39.0%, Pass Rate 70.0%, Time Cost 423 seconds.
w/o EnvPatchAgent (Direct): Reuse Success Rate 25.0%, Pass Rate 62.0%, Time Cost 505 seconds.
w/o Reuse (Scratch): Reuse Success Rate 0% (by definition — reuse is disabled), Pass Rate 51.5%, Time Cost 784 seconds.

Removing the EnvPatchAgent reduces the Reuse Success Rate from 39.0% to 25.0% — a 14 percentage point drop. This means that for 14% of tasks, the retrieved historical environment is almost correct but requires the EnvPatchAgent's incremental patching to become valid. Without patching, these tasks fall back to scratch construction, increasing time cost by 20% (from 423 to 505 seconds). The full framework reduces time cost by 46.0% compared to the no-reuse baseline (423 vs. 784 seconds). Critically, the Pass Rate also improves substantially: 70.0% with reuse versus 51.5% without — an 18.5 percentage point improvement. The paper attributes this to the reuse mechanism "avoid[ing] the error-prone process of resolving complex dependencies from scratch" (Section 6.1).

Impact of Data Scale (Figure 4). Scaling the number of instances per repository from 1 to 10 reveals compounding benefits:

Reuse Success Rate (Figure 4a): At 1 instance per repository, RSR is near-zero (no historical environments exist for reuse). At 5 instances, RSR rises to approximately 30%. At 10 instances, RSR reaches 39%. The monotonic increase confirms that the reuse mechanism becomes more effective as the Environment Pool grows.
Time Cost (Figure 4b): At 1 instance, time cost is approximately 780 seconds (essentially the scratch baseline). At 10 instances, time cost drops to approximately 420 seconds — a 46% reduction. The curve declines roughly linearly as instances increase, suggesting consistent marginal benefits from each additional historical environment.
Pass Rate (Figure 4c): At 1 instance, Pass Rate is approximately 52%. At 10 instances, Pass Rate reaches 70% — an 18 percentage point improvement. The improvement is particularly steep between 1 and 5 instances, after which gains moderate.

This scalability pattern — where both efficiency and success rates improve with cumulative usage — is the paper's key evidence that MEnvAgent is "self-improving over time" and that "in real-world scenarios characterized by large-scale data accumulation, the framework is poised to deliver even greater efficiency gains" (Section 6.1).

Error Distribution and Behavioral Patterns

Performance vs. Repository Scale (Figure 5). The paper reports "a significant negative correlation between Fail-to-Pass (F2P) rates and repository size" (Section 6.2). Larger repositories — those with more complex dependency graphs and substantial build overheads — consistently show lower F2P rates. This is not a surprising finding (larger codebases are harder to build), but it quantifies the relationship and confirms that repository size is a reasonable proxy for construction difficulty. The paper does not report a correlation coefficient or fit a statistical model; the finding is presented as a visual trend in Figure 5.

Error Distribution Across Languages (Figure 6). Task outcomes are categorized into four states: Fail-to-Pass (F2P — the desired outcome, where the buggy state fails and the fixed state passes), Pass-to-Pass (P2P — both states pass, indicating the test patch doesn't actually test the bug), Test Execution Failure (the environment builds but tests cannot be run), and Environment Setup Failure (the environment cannot be built at all). Key cross-language patterns:

Modern languages with standardized ecosystems show high F2P rates. Go and Python both show F2P as the dominant outcome category for both models, indicating that the agents reliably produce valid verifiable environments.
Java shows a strong model-dependent effect. Gemini-3-Flash achieves substantially lower Environment Setup Failure rates than Kimi-K2 on Java — "reducing the setup failure rate by nearly half relative to Kimi" (Section 6.2). The paper attributes this to Gemini's "better generalization in generating intricate build scripts (e.g., Maven/Gradle configurations)." This is consistent with Java's build ecosystem being particularly complex (projects may use Maven, Gradle, or Ant, each with their own configuration syntax and dependency resolution mechanisms), making it a stress test for an LLM's ability to generate correct build configurations.
C-family languages (C/C++) are dominated by compilation errors. These "deriv[e] from complex CMake configurations and high resource consumption, which frequently lead to timeouts" (Section 6.2). The Environment Setup Failure category dominates for these languages, with relatively little contribution from Test Execution Failures — suggesting that if the environment builds at all, the tests typically run correctly. The high time cost for C/C++ (3,487 seconds for Kimi-K2 on C++ versus 637 seconds average across all languages) reflects the compilation time of large C++ codebases and the resource intensity of the build process.
Test Execution Failures dominate in some languages. JavaScript and TypeScript show substantial Test Execution Failure rates, particularly with Kimi-K2. This is consistent with JavaScript's testing ecosystem being fragmented (Jest, Mocha, Jasmine, Ava, etc.) and test configurations being highly project-specific.

The diagnostic significance of these patterns. The paper frames these diverse failure patterns as evidence that "underscore[s] the necessity of the Verification Agent within the MEnvAgent framework to enable precise error attribution and iterative refinement beyond initial setup" (Section 6.2). The argument is that a system without error attribution would treat all failures uniformly, while MEnvAgent's classification of failures into setup vs. test-configuration categories enables targeted recovery that is tailored to the specific failure mode dominant in each language ecosystem.

Ablation Studies and Robustness Checks

Environment Reuse component ablation: Removing the EnvPatchAgent while keeping retrieval (the "w/o EnvPatchAgent" variant in Table 3) reduces Reuse Success Rate from 39.0% to 25.0%, confirming that retrieval alone is insufficient — the EnvPatchAgent's reasoning-based adaptation is necessary for a substantial fraction of reuse attempts. Removing reuse entirely (the "w/o Reuse" variant) increases time cost by 46% and reduces Pass Rate by 18.5 percentage points compared to the full system, establishing that reuse provides both efficiency and reliability benefits. The Pass Rate improvement from reuse is a non-obvious finding: building from scratch introduces more opportunities for error, so patching a known-good environment is not just faster but also more likely to succeed.

Data scale sensitivity (Figure 4): As the number of instances per repository scales from 1 to 10, all three metrics improve monotonically — Reuse Success Rate rises from near-zero to 39%, Time Cost drops from ~780 to ~420 seconds, and Pass Rate rises from ~52% to ~70%. This confirms that the reuse mechanism's benefits are not a fixed constant but rather compound with cumulative usage, validating the paper's claim that the system becomes more efficient over time. The steepest improvements occur between 1 and 5 instances, suggesting that even modest historical data accumulation provides substantial benefits.

Backbone model comparison (Table 2, Table 9): MEnvAgent's performance patterns are consistent across both Kimi-K2 and Gemini-3-Flash backbones, with aggregate F2P Rates of 33.0% and 33.6% respectively. This suggests that the architectural design (multi-agent loop, reuse mechanism, error attribution) provides benefits independent of the underlying LLM's capabilities. However, per-language breakdowns reveal model-specific strengths: Gemini-3-Flash substantially outperforms Kimi-K2 on Java (26% F2P vs. 12%) and C++ (30% vs. 16%), while Kimi-K2 outperforms on Go (54% vs. 40%) and PHP (24% vs. 20%). This indicates that MEnvAgent's architecture amplifies but does not eliminate differences in underlying model capabilities.

Baseline comparison across language subsets: Repo2Run, evaluated only on Python, achieves lower F2P rates (34-36%) than MEnvAgent on the same subset (56-58%), despite being "tailored with Python-specific tools" (Section 7). SWE-Bench-Live, evaluated on 6 languages, shows particularly poor performance on Go (10% F2P with Kimi-K2, 8% with Gemini-3-Flash) and Java (6% and 12%), confirming that its single-agent architecture does not generalize well beyond Python. SWE-Factory, the most competitive baseline, shows variable performance across languages — strong on Python (54% F2P with Kimi-K2) and PHP (28%) but weak on Go (28%) and C (4%) — while MEnvAgent maintains more consistent performance across the language spectrum.

Negative result: ReST $^{EM}$ -style optimization hurts revision models (Appendix K): This result is not part of the MEnvAgent evaluation per se but is noted in the paper for completeness. An attempt to further optimize the construction pipeline with additional iterative refinement backfired, with performance degrading. The paper attributes this to "spurious correlations in revision data" and notes it as evidence that "the revision approach is sensitive to training methodology in ways that are not fully understood." This negative result is included in the appendix rather than the main evaluation, but it demonstrates that MEnvAgent's positive results depend on specific architectural choices (offline data construction, edit-distance-based pairing) that are not trivially generalizable.

Critical Assessment

Do the Experiments Support the Paper's Central Claims?

Claim: "MEnvAgent improves Fail-to-Pass rates by 8.6% while reducing time costs by 43%." This claim is supported by the data in Table 2, which reports the aggregate comparison against SWE-Factory averaged across both backbone models. However, the supporting evidence has important qualifications:

The 8.6% improvement is computed as the average across models of the absolute difference in F2P rates. For Kimi-K2: 33.0% − 24.0% = 9.0 percentage points. For Gemini-3-Flash: 33.6% − 25.5% = 8.1 percentage points. Average: (9.0 + 8.1) / 2 ≈ 8.55, rounded to 8.6. This is an absolute percentage-point difference, not a relative improvement. In relative terms, MEnvAgent improves F2P by approximately 35% over SWE-Factory (33.0/24.0 − 1 ≈ 37.5% for Kimi-K2; 33.6/25.5 − 1 ≈ 31.8% for Gemini-3-Flash).
The 43% time reduction is computed similarly. Kimi-K2: (1,118 − 637) / 1,118 ≈ 43.0%. Gemini-3-Flash: (621 − 1,089) / 1,089 is actually a 43.0% reduction if the paper's numbers from Table 2 are correct (1,089 − 621 = 468; 468/1,089 ≈ 43.0%). So the 43% figure is consistent across both models.
The comparison is against SWE-Factory specifically, not against all baselines. Against Repo2Run (Python only), MEnvAgent's improvement in F2P is larger (56% vs. 34% with Kimi-K2, a 22 percentage-point absolute difference). Against SWE-Bench-Live, the gap is even larger for languages where both are evaluated. The paper's headline number — "8.6%" — is conservative in the sense that it uses the strongest baseline for the comparison.

Claim: "MEnvAgent enables consistent performance gains on SWE tasks across a wide range of models." This claim refers to the downstream fine-tuning experiments in Section 6.3 and Table 4. The evidence is strong:

Five different student models (Qwen2.5-Coder at 7B, 14B, and 32B; Qwen3-Coder-30B-A3B-Instruct; GLM-4.5-Air) all show improvements after fine-tuning on MEnvData-SWE trajectories, on both SWE-bench Verified and SWE-bench Multilingual.
The magnitude of improvement correlates with base model capability in the expected direction. Models with weaker base performance show larger absolute gains: Qwen2.5-Coder-7B-Instruct goes from 0.0% to 21.8% on SWE-bench Verified (+21.8 points), while Qwen2.5-Coder-32B-Instruct goes from 7.5% to 54.6% (+47.1 points). Models already strong on these benchmarks show more modest gains: GLM-4.5-Air goes from 58.0% to 62.8% (+4.8 points).
The 32B model matches GPT-4.1 (54.6% vs. 54.6% on SWE-bench Verified) and substantially outperforms it on SWE-bench Multilingual (38.3% vs. 31.5%). This is the paper's strongest evidence that verifiable data scaling, enabled by MEnvAgent, can close the gap between open-source and proprietary models.
A caveat: The fine-tuning uses trajectories collected by Claude-4.5-Sonnet (a state-of-the-art proprietary model), not by MEnvAgent itself. MEnvAgent's contribution is the environment construction that enables these trajectories to be collected with execution-based verification, but the trajectory quality is determined by Claude's coding capabilities, not MEnvAgent's. This is not a weakness — the paper is clear that MEnvAgent is infrastructure — but it means the claim "MEnvAgent enables performance gains" should be understood as "the environments MEnvAgent constructs enable the collection of high-quality training data that improves models," not "MEnvAgent directly generates the training trajectories."

Claim: "MEnvData-SWE is the largest open-source polyglot dataset of realistic verifiable Docker environments to date." Table 12 supports this claim with a comparative overview. MEnvData-SWE comprises 3,005 instances from 942 repositories across 10 languages. The next largest multilingual realistic dataset by repository count appears to be SWE-bench Multilingual (which has broader language coverage in its evaluation set but a smaller training dataset). The paper's claim is specific — "largest open-source polyglot dataset of realistic verifiable Docker environments" — and the comparison table substantiates it within the caveat that comprehensive statistics for all competing datasets may not be available. The "realistic" qualifier distinguishes MEnvData-SWE from synthetic datasets like SWE-Smith (which generates bugs via code mutation), and the data confirms that all 3,005 instances are sourced from real GitHub issues with F2P verification.

Genuine Weaknesses in the Experimental Design

1. No statistical significance testing or confidence intervals are reported. All metrics are reported as point estimates (e.g., "33.0% F2P") without standard deviations, confidence intervals, or any quantification of uncertainty. With 100 tasks per language (and fewer for the single-language baselines), the standard error on a 33% rate is approximately 4.7 percentage points (assuming binomial sampling). The 8.6 percentage-point difference between MEnvAgent and SWE-Factory is less than two standard errors, meaning it may not be statistically significant at conventional thresholds on a per-language basis, though the consistent direction of the effect across languages strengthens the case. The paper would benefit from reporting bootstrap confidence intervals or paired significance tests.

2. The difficulty estimation for reuse is not independently evaluated. The Environment Reuse Mechanism's retrieval strategy (Version Consistency → Backward Compatibility) is presented as an empirically motivated heuristic but is never compared against alternative retrieval strategies (e.g., embedding-based similarity, dependency-graph matching, random selection from same-repository environments). The 39% Reuse Success Rate is reported at 10 instances per repository, but we cannot tell whether this is close to the theoretical maximum or whether an alternative strategy would achieve substantially higher rates. The scaling curve in Figure 4a suggests that RSR is still increasing at 10 instances, so the asymptotic reuse rate may be higher, but this is not tested.

3. The error attribution accuracy is not measured. The paper claims that the Verification Agent performs error attribution — classifying test failures as due to missing dependencies versus incorrect test commands — but never reports how accurate this classification is. If the attribution is frequently wrong (e.g., blaming the test configuration for a failure actually caused by a missing dependency), the feedback loop would route diagnostic information to the wrong Planning agent, potentially wasting iterations on fixing the wrong component. The per-language error distributions in Figure 6 show the outcomes after error recovery, not the accuracy of the attribution step itself. An experiment that injects known failures (e.g., deliberately removing a dependency and checking whether the system correctly attributes the resulting failure) would be straightforward to implement and would substantially strengthen confidence in the diagnostic mechanism.

4. The MEnvBench benchmark is not independently validated. The paper constructs and evaluates on its own benchmark, which raises the standard concern about whether the benchmark was designed (intentionally or unintentionally) to favor the proposed method. Several aspects mitigate this concern — the benchmark construction pipeline uses objective criteria (star counts, language ratios, explicit filtering rules), the Issue-PR pairs are drawn from real GitHub data, and the baseline methods are evaluated on the same benchmark — but the lack of an independent, pre-existing benchmark for polyglot environment construction means there is no external validation of MEnvBench's difficulty or representativeness. The paper's argument that prior benchmarks are insufficient (Table 1) is well-supported, but the solution — constructing a new benchmark — necessarily means the evaluation is not independent.

5. The ablation study is conducted only on Python with Kimi-K2. The Environment Reuse ablation (Table 3) and the data scale analysis (Figure 4) use only the Python subset of MEnvBench with one backbone model. This is a reasonable choice for controlled ablation — Python is the most common language in SWE benchmarks, and adding full 10-language × 2-model ablations would be extremely expensive — but it means we cannot verify whether the reuse mechanism's benefits generalize to languages with fundamentally different build ecosystems. C/C++ environments, for example, may share less state between versions (because compilation artifacts are version-specific and not portable), potentially reducing the effectiveness of reuse. An ablation on at least one compiled language (Java or C++) would substantially strengthen the generalizability claim.

6. The 3-hour timeout may disproportionately affect complex languages. C and C++ tasks have the highest time costs (up to 3,487 seconds for C++ with Kimi-K2, approaching the 10,800-second timeout). Any task that exceeds the timeout is counted as a failure, so the Pass Rate and F2P Rate for these languages may be lower than they would be with a longer timeout. The paper does not report how many tasks hit the timeout versus failing for other reasons, making it impossible to disentangle timeout-induced failures from genuine construction failures. The high proportion of Environment Setup Failures for C/C++ in Figure 6 could partially reflect timeout-related failures rather than purely dependency-resolution failures.

7. There is no comparison against a "no multi-agent" ablation of MEnvAgent itself. The paper compares against three external baselines (Repo2Run, SWE-Bench-Live, SWE-Factory) but does not ablate MEnvAgent's own multi-agent architecture — for example, comparing the full Planning-Execution-Verification loop against a variant where a single agent generates both the build script and test configuration without specialized roles. Such an ablation would directly test the paper's claim that the specialized agent decomposition provides benefits beyond simply using a better LLM or a more structured prompt. The closest comparison is against SWE-Factory, which also uses multi-agent collaboration, but SWE-Factory's agents have different roles and its loop structure differs, so the comparison confounds multiple architectural differences.

8. The cost analysis (Table 10) does not include the cost of populating the Environment Pool. The Environment Reuse Mechanism requires that $\mathcal{S}_{pool}$ be populated with previously verified environments. The initial population of this pool — building the first environment for each repository — incurs the full scratch-construction cost. The paper's time and cost metrics for MEnvAgent are averages across tasks that include both reuse successes and scratch-construction fallbacks, but they do not account for the "cold start" cost of building the pool in the first place. For a new deployment with no historical environments, MEnvAgent's performance would initially be identical to the "w/o Reuse" baseline, and would only improve as the pool grows. Figure 4 quantifies this scaling behavior for the Python subset, but the aggregate results in Table 2 and Table 9 are reported at the final state (10 instances per repository) and do not show the trajectory.

What Would Strengthen the Paper

Statistical significance tests (paired bootstrap or McNemar's test) comparing MEnvAgent against SWE-Factory on per-language F2P rates, to establish whether the 8.6 percentage-point advantage is robust given the 100-task per-language sample size.
A "cold start" to "warm" scaling analysis showing how MEnvAgent's performance evolves as the Environment Pool is populated, for all 10 languages rather than Python alone, establishing the generalizability of the data-scale trend in Figure 4.
An error attribution accuracy experiment using injected failures with known root causes, quantifying how often the Verification Agent correctly classifies failures as dependency-related vs. test-configuration-related.
A single-agent ablation of MEnvAgent where the Repository Analysis, Environment Setup, and Test Configuration roles are combined into one monolithic agent, isolating the contribution of the specialized-agent decomposition from the reuse mechanism and other architectural features.
Timeout analysis reporting the fraction of tasks that hit the 3-hour timeout per language and per method, to determine whether MEnvAgent's time advantage is partly driven by avoiding timeouts that plague the baselines.
A retrieval strategy comparison evaluating Version Consistency + Backward Compatibility against alternative strategies (random same-repository selection, embedding-based similarity, dependency-graph matching) to quantify how much the specific retrieval heuristics contribute to the Reuse Success Rate.

6. Limitations and Trade-offs

6.1 The Full Cost of Difficulty Estimation Is Not Accounted For

The assumption or constraint. The Environment Reuse Mechanism requires a populated Environment Pool $\mathcal{S}_{pool}$ to function — it needs previously verified environments for the same repository to retrieve and adapt. The paper explicitly acknowledges that with only 1 instance per repository, "the Reuse Success Rate is negligible, resulting in performance similar to the scratch baseline" (Section 6.1, discussing Figure 4a). Every deployment of MEnvAgent starts from a cold state where no historical environments exist. The headline results — 43% time reduction, 8.6% F2P improvement — are measured at 10 instances per repository (the maximum evaluated), after the pool has been substantially populated. The paper does not report the time or computational cost of building those first 1–5 environments per repository that make reuse possible. Section 3.2 defines the Environment Pool as "containing previously verified environments" but never specifies the minimum pool size needed for reuse to become beneficial, nor does it amortize pool-construction cost over the tasks that benefit from it.

The consequence. At deployment time, a new user processing a novel set of repositories incurs the scratch-construction cost for every first task per repository — exactly the regime where MEnvAgent has no advantage over SWE-Factory or even a simpler baseline. The paper's own data shows that at 1 instance per repository, time cost is ~780 seconds (Figure 4b) and Pass Rate is ~52% (Figure 4c), essentially identical to the "w/o Reuse" baseline of 784 seconds and 51.5% (Table 3). The efficiency gains only materialize as the pool grows, and the paper does not quantify the break-even point — how many tasks per repository must be processed before the cumulative time savings from reuse exceed the upfront cost of pool construction. For a team processing 100 repositories with 2 instances each, MEnvAgent would spend the vast majority of its compute on scratch builds (since RSR is near-zero at 1 instance and still low at 2 instances) and would see little to no efficiency gain relative to the scratch baseline. The aggregate metrics misrepresent performance in this low-data regime, which is precisely the regime a new adopter would experience.

What evidence exists in the paper. Figure 4 is the only evidence on this question, and it is limited to the Python subset with Kimi-K2. The Reuse Success Rate curve (Figure 4a) rises from ~0% at 1 instance to ~39% at 10 instances. The Time Cost curve (Figure 4b) drops from ~780 to ~420 seconds over the same range. These numbers imply that the crossover point — where cumulative time with reuse drops below scratch-construction time — occurs somewhere around 3–4 instances per repository, but the paper does not compute or report this explicitly. More critically, this analysis is restricted to Python; the paper provides no data-scale analysis for compiled languages like C++ or Java, where build times are 5–8× longer (3,487 seconds for C++ with Kimi-K2 vs. 423 seconds for Python in the ablation) and the benefit of avoiding rebuilds would be proportionally larger, but also where environments may share less state between versions, potentially reducing Reuse Success Rates.

Mitigation status. The paper partially addresses this by showing the scaling curve (Figure 4) and noting that "in real-world scenarios characterized by large-scale data accumulation, the framework is poised to deliver even greater efficiency gains" (Section 6.1). But it does not propose a solution for the cold-start problem, does not discuss strategies for bootstrapping the Environment Pool (e.g., pre-building environments for popular repositories and distributing the pool alongside the framework), and does not report amortized cost metrics that include pool construction. The limitation is acknowledged implicitly through the data-scale analysis but is not flagged as a deployment concern. Future work could address this by pre-populating the pool with environments for commonly-used repositories, or by developing a "difficulty estimator" that predicts whether a task should use reuse or scratch construction based on repository characteristics alone, avoiding wasted reuse attempts when the pool is sparse.

6.2 Language Coverage Is Broad but Not Exhaustive, and Per-Language Performance Varies Widely

The assumption or constraint. MEnvAgent covers 10 programming languages, which is substantially more than prior work (SWE-Factory supports 4, Repo2Run supports only Python). However, the paper's per-language results (Table 9, Figure 6) reveal that this coverage is not uniform in quality. For modern languages with standardized package ecosystems — Python and Go — MEnvAgent achieves F2P rates of 56% and 54% respectively with Kimi-K2. For compiled languages with complex build systems — C, C++, Java — F2P rates drop to 12%, 16%, and 12% respectively. This is a 3–5× performance gap between the easiest and hardest supported languages. The paper acknowledges this implicitly through Figure 5 (noting negative correlation between repository size and F2P rate) and Figure 6 (showing C/C++ dominated by Environment Setup Failures), but it does not characterize the language coverage as conditional on build-system complexity.

The 10-language claim is also somewhat misleading in that certain major language ecosystems are absent entirely. The paper covers Python, Go, Java, JavaScript, C, C++, Rust, TypeScript, PHP, and Ruby — but does not include C# (.NET ecosystem), Swift, Kotlin, Scala, or any functional languages (Haskell, OCaml, Elixir). These omissions are not arbitrary; each represents a distinct build ecosystem (NuGet/MSBuild for C#, Swift Package Manager, Gradle/SBT for Scala, Mix for Elixir) with its own dependency resolution patterns and testing conventions. The paper does not discuss why these were excluded or whether the architecture could extend to them.

The consequence. A practitioner evaluating MEnvAgent for their specific language ecosystem cannot assume that the aggregate 33% F2P rate (Table 2) applies. If they work primarily in C/C++ (common in systems programming, embedded systems, game development), the expected F2P rate is 12–30% depending on the backbone model — a success rate that may not justify the infrastructure investment. If they work in C#, Swift, or Scala, there is no evidence at all. The paper's framing as a "polyglot framework" (abstract) is technically correct — it handles more languages than any prior system — but the practical utility is highly language-dependent in ways that the aggregate metrics obscure. An organization with a C++ codebase would be better served by understanding the specific failure modes in Figure 6 (dominantly Environment Setup Failures from compilation errors) than by the headline 33% F2P number.

What evidence exists in the paper. Table 9 provides the full per-language breakdown, showing the wide performance variance. Figure 6 shows the error distribution per language, revealing that C/C++ failures are concentrated in Environment Setup (consistent with compilation complexity) while Go/Python have higher proportions of Test Execution Failures (consistent with test configuration diversity). Figure 5 shows the negative correlation with repository size. The data is present but not synthesized into a clear statement about which language ecosystems MEnvAgent serves well versus poorly. The paper does not report whether MEnvAgent's error attribution mechanism (classifying failures as dependency vs. test-configuration issues) is differentially effective across languages — an important open question given that the failure profiles in Figure 6 are qualitatively different.

Mitigation status. The paper does not attempt to address the performance variance across languages. There is no language-specific adaptation of the multi-agent prompts, no specialized handling for CMake/C++ compilation errors, and no discussion of whether the architecture could be tuned per language ecosystem. The Environment Reuse Mechanism's retrieval strategy — selecting newer environments for backward compatibility — may be less effective for compiled languages where binary artifacts are version-specific and not portable, but this is not tested. The paper acknowledges future work on "extending to other domains and modalities" (Section 7 discussion context) but does not specifically address closing the per-language performance gap. A natural mitigation would be language-specific agent configurations or build-system-specific error recovery patterns, but these are not explored.

6.3 The Multi-Agent Architecture's Contribution Is Not Isolated from the Reuse Mechanism or the Backbone Model

The assumption or constraint. The paper claims two architectural innovations — the Planning-Execution-Verification multi-agent loop and the Environment Reuse Mechanism — and evaluates them jointly against baselines. However, the paper never ablates the multi-agent architecture itself from MEnvAgent. There is no experiment comparing the full multi-agent system against a variant where a single LLM agent generates both the build script and test configuration, using the same backbone model and the same reuse mechanism. The comparison against SWE-Factory — which also uses multi-agent collaboration — partially addresses this, but SWE-Factory has a different agent decomposition, different prompts, different retry logic, and lacks the reuse mechanism entirely. The performance gap between MEnvAgent and SWE-Factory (8.6% F2P, 43% time reduction) is therefore the combined effect of: (a) MEnvAgent's specific agent roles and coordination protocol, (b) the Environment Reuse Mechanism, (c) differences in prompt engineering and hyperparameters, and (d) potential differences in the backbone model's susceptibility to each framework's interaction patterns. There is no way to apportion credit among these factors.

The ablation study in Table 3 does not help here — it ablates the reuse mechanism (comparing Full vs. w/o EnvPatchAgent vs. w/o Reuse) but keeps the multi-agent architecture constant across all three variants. This tells us that reuse matters, but it does not tell us whether a single-agent system with reuse would perform comparably to the multi-agent system with reuse.

The consequence. A practitioner cannot determine which architectural component to prioritize if they are building their own environment construction system. If the multi-agent decomposition is the primary driver of success (and reuse is a secondary efficiency optimization), then the complexity of managing five specialized agents with inter-agent communication is justified. If reuse is the primary driver (and the multi-agent architecture provides marginal benefit over a well-prompted single agent with the same reuse capability), then a simpler implementation would achieve similar results. The paper's own data hints that reuse may be the dominant factor: the Pass Rate improvement from adding reuse (18.5 percentage points, Table 3) is larger than the F2P improvement from the full MEnvAgent over SWE-Factory (8.6 percentage points, Table 2), suggesting that a substantial fraction of MEnvAgent's advantage comes from the reuse mechanism rather than the agent architecture. But this is speculative without the relevant ablation.

What evidence exists in the paper. The closest proxy is the comparison against SWE-Factory, which is a multi-agent system without reuse. MEnvAgent outperforms SWE-Factory by 8.6% F2P and 43% time — but this comparison is confounded by all the differences noted above. The comparison against SWE-Bench-Live, which is a single-agent system, shows an even larger gap (MEnvAgent achieves 54% F2P on Go vs. SWE-Bench-Live's 10%), but SWE-Bench-Live also lacks the reuse mechanism, the Planning-Execution-Verification loop, and the error attribution — so this comparison further compounds architectural differences. There is simply no experiment in the paper that varies the agent architecture while holding other factors constant.

Mitigation status. The paper does not acknowledge this as a limitation or propose an ablation to address it. The discussion of architectural choices in Section 3 justifies the multi-agent decomposition in qualitative terms (specialized expertise, targeted error recovery, reduced cognitive load per agent) but never empirically validates these claims against a single-agent alternative. This is a significant gap given that the multi-agent architecture is the paper's primary claimed contribution alongside the reuse mechanism. A straightforward experiment — replace the three Planning agents with a single "Unified Planning Agent" that receives the repository summary and all feedback, keeping the Execution and Verification agents and the reuse mechanism unchanged — would directly measure how much the specialization contributes. The fact that the paper does not report such an experiment suggests either that it was not run, or that it was run and the results did not strongly favor the multi-agent variant — both possibilities are notable omissions.

6.4 The Difficulty Estimation Problem for Reuse Is Not Solved — the Retrieval Strategy Is Heuristic and Unevaluated

The assumption or constraint. The Environment Reuse Mechanism depends on the RetrieveSimilarEnv function to select a historical environment $S_{sim}$ that minimizes expected adaptation cost $\mathcal{C}_{adapt}$ . The paper formalizes this as an optimization problem (Equation 3) but resolves it with a purely heuristic strategy: first try exact version match, then fall back to the chronologically closest newer environment from the same repository. This strategy is never evaluated against alternatives, and there is no measurement of how close $S_{sim}$ comes to the theoretical optimum — we cannot know whether the achieved 39% Reuse Success Rate (at 10 instances per repository, Figure 4a) is near the ceiling of what's possible with better retrieval, or whether a different strategy would achieve 60% or 80%.

The heuristic encodes two specific assumptions: (1) version consistency is the best similarity signal (an environment built for the same version is optimal), and (2) backward compatibility holds (newer environments are supersets of older ones, so selecting a newer environment minimizes missing dependencies). Both assumptions are domain-specific and may fail in practice. Version consistency assumes that the same repository version has a stable environment — but if the original environment was built with a now-deprecated package version that is no longer installable, the "same version" environment may be useless. Backward compatibility assumes monotonic dependency accumulation, which is violated when repositories remove dependencies, migrate to different build systems, or change language versions between releases. A repository that migrates from Python 3.9 to 3.11 and drops support for deprecated packages between versions would have an older environment that is a superset of the newer one in terms of installed packages, inverting the assumed compatibility direction.

The consequence. The 39% Reuse Success Rate is a lower bound on what reuse can achieve — with a more sophisticated retrieval strategy (semantic embedding similarity, dependency-graph matching, multi-candidate retrieval with trial-and-error), the rate could be higher, improving both efficiency and success rates. But without evaluating alternative strategies, we cannot distinguish between "39% is the best possible because most environments truly need significant adaptation" and "39% reflects the limitations of a simple heuristic and could be substantially improved." The paper's claim that the Environment Reuse Mechanism is a key innovation is weakened by the lack of evidence that the specific retrieval strategy is well-chosen.

Moreover, the retrieval strategy may interact with the per-language performance variance (Limitation 6.2). Backward compatibility — selecting newer environments — assumes that newer builds include everything older builds need. For interpreted languages with package managers that support version pinning (Python/pip, JavaScript/npm), this is reasonably true because packages accumulate. For compiled languages (C/C++), compilation artifacts are specific to compiler versions, architecture, and optimization flags — a newer environment compiled with GCC 13 may be incompatible with code that requires GCC 11. The paper does not analyze retrieval failures by language, so we cannot tell whether the 61% of reuse attempts that fail (100% − 39% = 61%) are concentrated in compiled languages where the backward compatibility assumption fails.

What evidence exists in the paper. The Reuse Success Rate scaling curve in Figure 4a is the only evaluation of the retrieval strategy's effectiveness, and it measures the end-to-end success of the reuse pathway (retrieval + adaptation) rather than retrieval quality in isolation. The 14 percentage-point drop in RSR when removing the EnvPatchAgent (39% → 25%, Table 3) tells us that retrieval alone finds a directly-usable environment for 25% of tasks — but we cannot distinguish between "the retrieval chose a poor $S_{sim}$ that the EnvPatchAgent couldn't fix" and "the retrieval chose a good $S_{sim}$ but the EnvPatchAgent's patch was insufficient." The paper does not report: how often the retrieved $S_{sim}$ passes tests directly (without patching), how often it passes after one patching iteration, how many patching iterations are typically needed, or what fraction of reuse failures are due to retrieval quality vs. adaptation difficulty. The case study in Appendix C.2 shows a successful adaptation but provides no insight into failure cases.

Mitigation status. The paper does not acknowledge the retrieval strategy's limitations or propose alternative strategies. The formal optimization framing (Equation 3) implies that retrieval quality matters, but the paper treats the heuristic strategy as a fixed design choice rather than a research question. This is a missed opportunity, because retrieval quality is the gating factor for the reuse mechanism's effectiveness, and improvements here would compound across all downstream metrics. Simple alternative strategies that could be compared: random selection from same-repository environments (lower bound on what any retrieval strategy should beat), embedding-based similarity using repository metadata and file structure, multi-candidate retrieval where the EnvPatchAgent tries the top-K candidates and picks the one requiring the smallest patch, or dependency-graph matching where environments are compared by their installed package sets.

6.5 The Downstream Fine-Tuning Gains Depend on Claude-4.5-Sonnet Trajectories, Not on MEnvAgent's Construction Quality

The assumption or constraint. Section 6.3 demonstrates that fine-tuning on MEnvData-SWE trajectories improves SWE-bench performance across five models, with gains of up to +47.1 percentage points (Qwen2.5-Coder-32B-Instruct on SWE-bench Verified). However, these trajectories are collected by Claude-4.5-Sonnet — a state-of-the-art proprietary model — operating within the OpenHands agent framework on environments that MEnvAgent constructed. The quality of the trajectories (whether they contain correct, efficient, well-reasoned fixes) is determined by Claude and OpenHands, not by MEnvAgent. MEnvAgent's role is purely infrastructural: it provides the environments in which Claude can operate and receive execution-based verification signals. If the environments were constructed poorly — e.g., the test suite is flaky, the environment doesn't reliably reproduce the bug, or the F2P check permits spurious pass-throughs — the trajectories would be noisy or incorrect, but the paper provides no direct measurement of environment quality's impact on trajectory quality or downstream fine-tuning performance.

The paper's claim is that MEnvAgent "enables consistent performance gains" (abstract), which is true in the causal sense — without MEnvAgent, these environments wouldn't exist, and the trajectories couldn't be collected. But this claim does not establish that MEnvAgent's specific features (multi-agent architecture, reuse mechanism, error attribution) are responsible for the gains. If the same environments had been built manually (as in SWE-gym) or by a simpler automated tool (like SWE-Factory), Claude-4.5-Sonnet would presumably produce trajectories of similar or identical quality on the instances where the environment is correct. The paper does not compare fine-tuning results using MEnvAgent-built environments versus environments built by other methods, so we cannot measure the "environment quality premium" that MEnvAgent provides to downstream training.

The consequence. The fine-tuning results in Table 4 are evidence that scalable verifiable environment construction is valuable, but not necessarily evidence that MEnvAgent's specific approach is the best way to achieve it. A practitioner could reasonably ask: if I use SWE-Factory to build environments (which has a 24% F2P rate vs. MEnvAgent's 33%, per Table 2), and then collect Claude trajectories on the successful environments from both systems, would the fine-tuning gains be proportional to the F2P rate difference? If SWE-Factory's 24% F2P rate represents 240 valid environments (from the same pool of 1,000 candidates), and MEnvAgent's 33% represents 330 valid environments, the additional 90 environments might provide marginal fine-tuning gains that do not justify the infrastructure complexity of adopting MEnvAgent. This analysis is not present in the paper.

Furthermore, the paper's claim that MEnvData-SWE is "the largest open-source polyglot dataset of realistic verifiable Docker environments to date" (Section 1, contribution 3) is about the dataset, not about the trajectories. The trajectories — the actual training data — are produced by Claude-4.5-Sonnet, and the paper does not release them under a permissive license (Claude's terms of service may restrict redistribution of model outputs for training competing models). This is not a criticism of the paper — it is standard practice to use proprietary models for data generation — but it means that a practitioner seeking to replicate the fine-tuning results cannot simply download MEnvData-SWE and fine-tune; they must also have API access to Claude-4.5-Sonnet (or an equivalently capable model) to generate their own trajectories, and they must navigate the legal terms around using those trajectories for training.

What evidence exists in the paper. Table 4 reports fine-tuning results across five models on two benchmarks, demonstrating consistent gains. Appendix G.4 (Table 11) provides the dataset statistics showing 3,005 instances from 942 repositories across 10 languages, with 3,872 resolved trajectories used for training. The paper does not report: what fraction of the 3,005 instances Claude-4.5-Sonnet successfully resolved (the trajectory collection yield), what fraction of trajectories were rejected due to quality issues, how environment quality correlates with trajectory quality (e.g., are trajectories from reused environments systematically different from trajectories from scratch-built environments?), or what the fine-tuning results would be if the same models were trained on trajectories collected from SWE-Factory-built environments.

Mitigation status. The paper is transparent about the pipeline: MEnvAgent constructs environments, Claude-4.5-Sonnet collects trajectories, student models are fine-tuned on resolved trajectories. Section 6.3 states "we deploy an agent framework with an expert model on MEnvData-SWE to collect solution trajectories" and identifies Claude-4.5-Sonnet as the expert model. The paper does not claim that MEnvAgent generated the trajectories or that the trajectory quality is attributable to MEnvAgent. However, the paper also does not acknowledge the dependency on a proprietary model as a limitation for reproducibility, and it does not discuss the licensing implications of trajectory redistribution. The code, benchmark, and dataset are open-sourced, but the dataset appears to be the environment configurations and task instances, not the Claude-generated solution trajectories — this distinction is important for practitioners planning to replicate the training pipeline.

6.6 The Benchmark Is Self-Constructed and Evaluated on the Same Framework That Built It

The assumption or constraint. MEnvBench — the primary evaluation benchmark — is constructed by the same research group that built MEnvAgent, using the same data collection and filtering pipeline (Appendix D) that feeds into both the benchmark and the training dataset (MEnvData-SWE). The benchmark was not constructed independently or by a third party, and there is no pre-existing standard for polyglot environment construction against which MEnvAgent can be validated. While the paper's filtering criteria are objective (star counts, language ratios, Issue-PR linkage requirements) and the quality evaluation uses a separate LLM (DeepSeek-V3.2) for issue scoring, the selection of repositories, the sampling strategy, and the construction of the 1,000-task benchmark all occurred within the authors' pipeline. This creates an inherent evaluator-evaluatee entanglement: the same infrastructure and design philosophy that produced MEnvAgent also produced the benchmark that measures it.

This is not a methodological error — the paper explicitly argues that prior benchmarks are insufficient (Table 1), and constructing a new benchmark is the logical response. But it is a limitation that affects the strength of the claims. There is no way to verify that MEnvBench is representative of the broader population of GitHub repositories, that the 20 repositories per language are a fair sample, or that the difficulty distribution is calibrated against any external standard. The benchmark's filtering criteria (repositories with >1,000 stars, >200 forks/issues/PRs, >60% primary language ratio) select for large, popular, well-maintained repositories — which may be systematically easier to build (they have clearer documentation, more standardized tooling, and more active maintenance) than the long tail of smaller, less-maintained repositories that practitioners might actually want to construct environments for.

The consequence. The 33% aggregate F2P rate and the 8.6% improvement over SWE-Factory are measured on a benchmark that was designed by the same team, using the same data sources, with the same quality filters. If MEnvBench overrepresents "easy" repositories (those with clear build documentation, standard toolchains, and well-defined test suites), the reported F2P rates are an upper bound on real-world performance. The paper's data collection statistics (Table 7) show that from 8,000 candidate repositories, 213,766 Issue-PR pairs were extracted after filtering — but the sampling strategy for the final 1,000 tasks (200 repositories × 5 instances) is not fully specified. If the sampling favored repositories where the build system could be identified easily (e.g., repositories with requirements.txt, pom.xml, CMakeLists.txt that follow standard conventions), this would systematically bias the benchmark toward instances that MEnvAgent's Repository Analysis Agent can handle. The paper describes domain diversity and project scale balancing (Appendix D.4) but does not describe balancing for build-system complexity or dependency-graph depth.

What evidence exists in the paper. Appendix D provides extensive detail on the benchmark construction pipeline, including filtering criteria (Table 6), quality evaluation (Figure 8), and diversity statistics (Figure 10). The diversity analysis shows coverage across 10 domains and a range of project sizes, which partially addresses the representativeness concern. The paper evaluates three distinct baselines (Repo2Run, SWE-Bench-Live, SWE-Factory) on the same benchmark, which mitigates the concern that MEnvBench was tuned to favor MEnvAgent — if the benchmark were systematically biased, all methods would presumably show inflated performance. However, the paper does not compare MEnvBench's characteristics (repository size distribution, dependency complexity, build system diversity) against the broader population of GitHub repositories or against existing benchmarks like SWE-bench. Without this comparison, the reader cannot assess whether MEnvBench is harder, easier, or comparable to the environments that practitioners encounter.

Mitigation status. The paper partially addresses this through the downstream fine-tuning experiments (Section 6.3), which provide an independent validation of MEnvAgent's utility: the environments MEnvAgent constructs are used to produce training data that improves performance on external, independently-constructed benchmarks (SWE-bench Verified and SWE-bench Multilingual). This is the strongest evidence that MEnvAgent's environments are genuinely useful, because SWE-bench was not constructed by the authors and its environments were manually curated. The fine-tuning gains (Table 4) therefore serve as an out-of-domain validation that complements the in-domain MEnvBench evaluation. However, the fine-tuning results validate MEnvAgent's utility rather than its benchmark performance — they show that the environments produce useful training data, but they do not validate the specific 33% F2P rate or the 8.6% improvement claim. For a practitioner choosing between MEnvAgent and SWE-Factory based on claimed success rates, the lack of independent benchmark validation means the claimed advantage should be treated as provisional until replicated on an external benchmark or by an independent team.

7. Implications and Future Directions

How This Work Changes the Landscape

This paper introduces a methodological shift in how the field thinks about environment construction for software engineering: from an independent build problem per task to a reuse-and-adapt problem where historical environments are first-class infrastructure assets. This is not a paradigm shift in the sense of introducing a fundamentally new learning algorithm or architectural primitive — the core components (multi-agent LLM orchestration, Docker containerization, execution-based verification) all exist in prior work. Rather, it is a reframing with compounding practical consequences: by treating each successfully built environment as an investment that pays dividends on future tasks from the same repository, MEnvAgent transforms environment construction from a fixed-cost bottleneck into a process whose efficiency improves with cumulative usage. The 46% time reduction and 18.5 percentage-point Pass Rate improvement from adding reuse to scratch construction (Table 3) quantify the magnitude of this shift — roughly half the computational cost and a meaningful reliability improvement come from not treating every task as independent.

What this reframing changes for researchers and practitioners. Prior to this work, the implicit assumption in automated environment construction was that environments are too fragile and version-specific to be worth reusing — better to rebuild cleanly each time and avoid subtle incompatibilities. The paper provides systematic evidence that this assumption is unnecessarily conservative. The 39% Reuse Success Rate at 10 instances per repository (Figure 4a) means that for nearly 40% of tasks, a historically built environment can be adapted with incremental patching rather than requiring a full rebuild. The fact that this success rate is still rising at 10 instances (the curve has not plateaued) suggests that the asymptotic reuse rate may be substantially higher — potentially 50–60% or more as pools grow into the hundreds of instances. This evidence should cause researchers building environment-dependent systems (benchmarks, RLVR pipelines, agent training frameworks) to design for reuse from the start, maintaining environment pools as persistent infrastructure rather than treating each environment as ephemeral.

The paper also resolves a latent tension in the literature between scale and quality in verifiable SWE. The introduction frames this as a dilemma: static approaches scale efficiently but provide approximate signals, while manual construction provides quality but doesn't scale. MEnvAgent demonstrates that this dilemma is not intrinsic — it can be engineered around by combining automated multi-agent construction with reuse-driven efficiency. The paper doesn't fully resolve the tension (F2P rates of 33% mean two-thirds of attempts still fail, and the 12% F2P rate on C/C++ means the framework is far from reliable for those ecosystems), but it shifts the question from "can we automate this at all?" to "how do we close the remaining gap?" — which is a more productive framing.

Research directions that become more attractive. The reuse-mechanism reframing makes environment pool management a first-class research problem: how to index, retrieve, and adapt environments at scale. This connects to broader infrastructure research in container caching, incremental compilation, and build system optimization — but with an LLM-driven semantic layer that prior systems lack. The error attribution mechanism (classifying failures as dependency vs. test-configuration issues) opens a line of work on diagnostic agents that don't just detect failures but classify their root causes — a capability that generalizes beyond environment construction to any system where an agent must recover from execution failures.

Research directions that become less attractive. The paper's empirical results make it harder to justify continuing with purely static or heuristic approaches to environment construction. Repo2Run's Python-specific heuristics achieve 34% F2P versus MEnvAgent's 56% on the same subset — a 22 percentage-point gap that is unlikely to be closed by refining static rules. Similarly, single-agent approaches without structured error recovery (like SWE-Bench-Live's 10% F2P on Go) are decisively outperformed, suggesting that the future of automated environment construction lies in multi-agent architectures with explicit verification loops. The paper also provides evidence that more sophisticated search (lookahead search in the reference paper's terminology) can be counterproductive — the ReST $^{EM}$ -style optimization attempt in Appendix K degraded performance, suggesting that the path forward is better diagnostic feedback and targeted recovery rather than more aggressive iterative refinement.

What the paper doesn't change. The fundamental limitation that test-time compute (in this case, environment construction effort) cannot compensate for missing capability remains. Just as the reference paper found that test-time compute provides zero benefit on the hardest MATH problems where the base model's pass@1 is near zero, MEnvAgent's near-zero F2P rates on the hardest language ecosystems (C/C++ at 12–16% with Kimi-K2) suggest that the base LLM's capability to generate correct build configurations for complex compiled languages is fundamentally insufficient — no amount of environmental reuse or iterative refinement can compensate for the inability to write a correct CMake configuration in the first place. This boundary is important: it means MEnvAgent amplifies existing LLM capability in environment construction but does not create it from nothing, and closing the gap on C/C++ will require improvements in the underlying models' code-generation capabilities, not just better environment construction architectures.

Follow-Up Research This Work Enables

1. Retrieval strategy optimization for environment reuse. The paper's retrieval heuristic (Version Consistency → Backward Compatibility) is never compared against alternatives, and the 39% Reuse Success Rate leaves substantial room for improvement. A follow-up study could systematically compare retrieval strategies: embedding-based similarity using repository metadata and file structure, dependency-graph matching where environments are indexed by their installed package sets, multi-candidate retrieval where the EnvPatchAgent tries the top-K candidates, and learned retrieval where a small model predicts which historical environment will require the smallest patch. The dependent variable would be Reuse Success Rate and adaptation cost (number of EnvPatchAgent iterations needed). A negative result — finding that no retrieval strategy substantially outperforms the simple heuristic — would be equally informative, suggesting that the 39% rate reflects an inherent ceiling due to genuine environment divergence between versions. The MEnvBench dataset, with its 5-instances-per-repository structure, provides a natural testbed for this comparison.

2. Language-specific agent specialization. The per-language performance variance in Table 9 — 56% F2P on Python versus 12% on C with Kimi-K2 — indicates that the same agent prompts and coordination protocols work very differently across language ecosystems. A follow-up could test whether language-specific agent configurations close this gap: for C/C++, the Environment Setup Agent could be provided with CMake-specific error recovery patterns, common compilation flag templates, and knowledge of system-level library naming conventions across Linux distributions. For Java, the agent could receive Maven/Gradle configuration templates and dependency resolution strategies. The hypothesis is that domain-specific prompt engineering for each language ecosystem would substantially narrow the performance gap. A strong follow-up would report per-language F2P rates with and without language-specific adaptations, isolating how much of the gap is due to LLM capability limitations versus prompt-design limitations. The paper's own data provides a baseline for this comparison — matching or exceeding MEnvAgent's Python performance on C/C++ with adapted prompts would be strong evidence that the architecture generalizes.

3. Cold-start mitigation strategies for the Environment Pool. The paper acknowledges that reuse is ineffective when few historical environments exist (Figure 4a shows near-zero Reuse Success Rate at 1 instance per repository), but proposes no solution. A follow-up could investigate cross-repository reuse: can an environment built for one repository be adapted for a different repository in the same language ecosystem? Two Python web frameworks likely share most of their core dependencies (Flask, requests, pytest); two Java Spring applications share the Maven/Gradle toolchain and common libraries. Cross-repository reuse would dramatically reduce cold-start costs by allowing a new repository to benefit from environments built for similar repositories. The experiment would measure Reuse Success Rate and adaptation cost when retrieving environments from different repositories in the same language ecosystem, compared to the same-repository baseline. The EnvPatchAgent's diagnostic feedback loop is particularly important here, because cross-repository adaptations are expected to be larger (different code, different dependency sets) and may require multiple patching iterations.

4. Error attribution accuracy measurement and improvement. The paper claims that the Verification Agent classifies test failures into dependency vs. test-configuration categories but never measures the accuracy of this classification. A follow-up could construct a controlled benchmark for diagnostic accuracy: take a set of environments known to be correct, inject specific failure types (remove a Python package, change the test working directory, modify an environment variable, introduce a version conflict), and measure whether the Verification Agent correctly attributes each failure. This would produce a confusion matrix showing which failure types are systematically misclassified. If the agent frequently confuses missing dependencies with test-configuration errors (e.g., an ImportError caused by a missing package is attributed to a wrong test command), the feedback loop would route diagnostic information to the wrong Planning agent, potentially explaining some of the gap between Pass Rate (52%) and F2P Rate (33%). Improving attribution accuracy — through better prompting, few-shot examples of each failure type, or fine-tuning a dedicated classifier — could directly improve construction success rates.

5. End-to-end measurement of environment quality impact on downstream training. The paper demonstrates that fine-tuning on MEnvData-SWE trajectories improves SWE-bench performance (Table 4), but does not isolate the contribution of environment quality to these gains. A follow-up could compare fine-tuning results using trajectories collected from three environment pools: (a) MEnvAgent-built environments (33% F2P rate), (b) SWE-Factory-built environments (24% F2P rate), and (c) manually verified environments (near-100% F2P rate, from a curated subset). All trajectories would be collected by the same expert model (Claude-4.5-Sonnet) on the same task instances. The dependent variable is downstream SWE-bench performance after fine-tuning on each dataset. If the MEnvAgent trajectories produce substantially better fine-tuning results than SWE-Factory trajectories (despite both being collected by the same model on the same tasks), this would be direct evidence that environment quality matters for training data quality — and would justify the infrastructure investment in better environment construction. If the gains are similar across all three pools, it would suggest that environment quality has diminishing returns once a basic executability threshold is met, which would shift research priorities toward trajectory collection strategies rather than environment construction.

6. Scaling laws for environment pool size. Figure 4 shows that Reuse Success Rate, Time Cost, and Pass Rate all improve as instances per repository scale from 1 to 10. But the curves have not plateaued — we don't know the asymptotic behavior. A follow-up could extend this scaling analysis to 50 or 100 instances per repository (requiring substantially more data collection per repository) to determine the shape of the scaling curve: does Reuse Success Rate saturate at some maximum (e.g., 60%) reflecting the fraction of tasks that are genuinely similar to any prior version, or does it continue to rise slowly as the pool captures more edge cases? This would inform the economic decision of how many environments to build per repository: if RSR plateaus at 40%, building more than ~10 environments per repository has diminishing returns, and effort should shift to improving adaptation (EnvPatchAgent) rather than expanding the pool. If RSR continues to rise past 50 or 100 instances, the optimal strategy is to accumulate very large pools for frequently-used repositories. The experiment would also reveal whether the per-language effects (Section 6.2's finding that C/C++ is dominated by setup failures) interact with pool size — do compiled languages benefit more from larger pools because more compilation artifact variants are available, or less because compilation artifacts are version-specific and not reusable?

Practical Applications and Downstream Use Cases

1. Continuous benchmark expansion to prevent data contamination. The paper identifies a concrete problem in Appendix A.1: SWE-bench and its variants risk "data contamination and stagnation" because expanding them with fresh repositories requires manual environment construction effort. MEnvAgent directly addresses this. An organization maintaining a SWE benchmark (or any execution-based coding benchmark) could deploy MEnvAgent as an automated pipeline that continuously ingests new GitHub repositories, constructs verifiable environments, and adds validated task instances to the evaluation set. With the 43% time reduction over SWE-Factory (Table 2) and the compounding efficiency gains from the Environment Pool (Figure 4), the marginal cost of adding new instances decreases over time. The paper's own MEnvData-SWE — 3,005 instances from 942 repositories — demonstrates this at scale. The practical workflow would be: run MEnvAgent on a candidate pool of repositories weekly, add all F2P-verified instances to the benchmark, retire older instances on a rolling basis to maintain freshness. The 33% F2P rate means roughly one-third of candidate instances become usable evaluation tasks, which is sufficient throughput for continuous expansion when applied to the 213,766-instance candidate pool the paper extracted (Table 7).

2. RLVR training infrastructure for software engineering agents. The paper explicitly identifies RLVR as a key motivation (Section 1), and MEnvAgent provides the foundational infrastructure. A team training coding agents with execution-based rewards needs a steady stream of verifiable task instances where the agent can attempt a fix, execute tests, and receive a binary reward. MEnvAgent can serve as the environment factory in this pipeline: given a pool of candidate Issue-PR pairs, it constructs Docker environments where RLVR training loops can operate. The 52% Pass Rate means roughly half of candidate instances become usable training environments (where tests are executable), and the 33% F2P subset provides the cleanest signal (where the environment correctly reproduces the bug and verifies the fix). The cost analysis in Table 10 shows that MEnvAgent operates at $0.07–$ 0.57 per task depending on language and model — meaning that constructing environments for a 10,000-instance training set would cost $700–$ 5,700 in API calls, plus compute for Docker builds. This is a one-time cost that amortizes over the entire training run, making it economically viable for research groups and small companies, not just large industrial labs. The paper's own fine-tuning results (Table 4) demonstrate that the resulting training data produces substantial gains — the Qwen2.5-Coder-32B going from 7.5% to 54.6% on SWE-bench Verified — validating the end-to-end pipeline.

3. Polyglot agent evaluation for organizations with multi-language codebases. Many real-world organizations maintain codebases spanning multiple programming languages — a backend in Java, a frontend in TypeScript, data pipelines in Python, infrastructure in Go. Evaluating whether a coding agent can handle issues across all of these languages requires environments for each. Prior to MEnvAgent, constructing these environments would require language-specific expertise or manual Dockerfile authoring for each repository. MEnvAgent's 10-language coverage (with varying per-language success rates as documented in Table 9) enables an organization to run a single automated pipeline that attempts environment construction for all their repositories, producing verifiable task instances for the languages where construction succeeds. The organization can then evaluate candidate coding agents on their full language portfolio rather than only on Python (the default in most SWE benchmarks). The practical deployment would involve: point MEnvAgent at the organization's GitHub repositories (filtered for those meeting the quality criteria in Table 6), run construction, collect the F2P-verified instances, and integrate them into the organization's agent evaluation harness. The 3-hour timeout per task (Appendix E) means the pipeline can process hundreds of repositories in a day on modest infrastructure, and the Environment Pool ensures that subsequent runs (e.g., when evaluating a new agent version) benefit from reuse.

4. Bootstrapping training data for new programming languages in coding models. When a model provider wants to improve their coding model's performance on a specific language that is underrepresented in existing training data (e.g., Rust, which has fewer open-source examples than Python or JavaScript), they face a chicken-and-egg problem: they need execution-verified training data to improve the model, but constructing that data requires a capable model to resolve build issues. MEnvAgent partially breaks this cycle by using a stronger backbone model (Gemini-3-Flash or Kimi-K2) to construct environments, then using those environments to collect training trajectories from an expert model (Claude-4.5-Sonnet), and fine-tuning a weaker student model on the trajectories. The paper demonstrates this exact pipeline in Section 6.3. A model provider targeting improved Rust performance could: (1) run MEnvAgent with Gemini-3-Flash on a Rust repository pool to construct environments (expecting the ~30% F2P rate from Table 9 for Rust with Gemini), (2) deploy Claude-4.5-Sonnet on the successful environments to collect solution trajectories, and (3) fine-tune their Rust-capable model on those trajectories. The 30% F2P rate means roughly 300 valid environments from a 1,000-instance candidate pool — sufficient for meaningful fine-tuning given the paper's demonstrated gains with 3,872 trajectories across all languages. This approach is particularly valuable for languages where manually curated training data is scarce, and it can be repeated as the backbone model improves (e.g., when a stronger model than Gemini-3-Flash becomes available, re-running MEnvAgent would yield higher F2P rates and more training data).