Evaluation Scores Are Only Useful When They Match Their Target

A document evidence model agreed with reference labels on 36 out of 40 observations — a 90% accuracy rate. But opening the confusion matrix reveals a problem masked by that high score: it missed the only sample labeled "documented evidence." Based on a local prototype experiment by the author, this article discusses how the definition of an evaluation target determines what a score actually means.

What 90% Accuracy Conceals

The author built an assistive tool to help users locate and verify evidence in documents. The 40 observations came from 10 documents, 4 dimensions per document, with each dimension assigned one of four possible "document states": documented evidence, not located, explicitly missing, or ambiguous.

The model's overall agreement rate was 36/40, or 90%. But the confusion matrix revealed a critical failure: the model correctly reproduced all 33 samples of "not located," got only 3 of 6 "ambiguous" samples right, and predicted the single sample labeled "documented evidence" as "not located."

For an assistant meant to help users locate evidence, reproducing the dominant "not found" state while missing the only positive sample does not demonstrate usefulness. This is precisely the problem the title refers to: an evaluation score is only interpretable when it corresponds to the target it actually measures.

The Target Definition Is Itself Part of System Design

The author emphasizes that the reference labels in this experiment came from AI generation, without fresh independent human annotation. Therefore, 36/40 measures "the degree of reproduction of reference labels," not "the model's ability to locate document evidence." Conflating these two makes a single number carry meaning far beyond its evidentiary scope.

Each of the four document states requires precise interpretation. "Not located" describes the state revealed by existing documents and processes at that time — it cannot directly infer that someone lacks a particular skill. Documents may omit what a person actually possesses, extraction may fail, or relevant passages may use unexpected phrasing.

"Documented" likewise requires caution. A passage mentioning a tool does not equal a description of completed work; expressed "learning intent" and "practical evidence" are two different things. When conflicting passages exist, a human reviewer needs to step in rather than forcibly assigning a positive or negative label.

Class Support Must Be Presented Alongside Aggregate Metrics

The reference distribution of the author's 40 observations was highly imbalanced:

Reference State	Observations
Documented evidence	1
Not located	33
Explicitly missing	0
Ambiguous	6

This table directly explains where 36/40 comes from. More importantly, it exposes a fact masked by the aggregate metric: one of the four classes (explicitly missing) has no evaluation support at all. In a four-class macro-F1 calculation, that class's numerical contribution does not equal "performance measured on that state" — it has no evaluative foundation whatsoever.

The author wants reports to make "untested abilities" visible. Readers should be able to distinguish between two situations: "the method failed on these samples" and "this dataset simply didn't test this ability." These may look identical in an aggregate score, but their meanings are entirely different.

Macro-F1 and Class Support: Macro-F1 works by first computing the F1 (harmonic mean of precision and recall) for each class separately, then taking an equal-weighted average across all classes. Its key difference from micro-F1 and accuracy is that micro-F1 and accuracy are dominated by classes with large sample sizes, whereas macro-F1 gives every class equal voting weight regardless of sample count. So when a class (such as "explicitly missing" in this article) has zero observations, its F1 may formally be defined as 0 or simply skipped, but there is no basis whatsoever for estimating performance on that class — the denominator contains no evaluable samples. This is exactly why the author insists that "support must be presented alongside aggregate metrics": a macro-F1 number could come from "all four classes were tested but all performed poorly" or from "three classes were tested, one was not" — the two are indistinguishable when looking at the score alone. Presenting per-class observation counts (support) together with the confusion matrix and macro-F1 allows readers to judge whether a high score truly covers all classes or is merely propped up by the dominant class.

40 Rows Do Not Equal 40 Independent Documents

The 4 dimensions within the same document share text, formatting, extraction quality, and source context — the observations are correlated. Describing these 40 observations as 40 independent cases is misleading; randomly splitting rows and allowing dimensions from the same document to appear in both the training and evaluation sets carries the same risk — the model may see substantially identical underlying inputs on both sides.

The author recommends that future document-level evaluations group by source document before assigning splits, and that closely related versions and duplicate documents be handled the same way. The splitting unit should reflect how information flows across boundaries, not choose whichever unit makes the table easiest to divide.

This run has an even simpler limitation: all 40 observations are training observations. It demonstrated the technical learning process and exposed errors, but did not measure performance on unseen documents.

Data Leakage and Splitting Units: Machine learning evaluation assumes that evaluation samples are independent of each other and that no information from the evaluation set has flowed into the training process in any form. When multiple dimensions of the same document are randomly assigned to both training and evaluation sets, this assumption is broken: text, formatting, and extraction results the model saw on the training side reappear on the evaluation side in nearly identical form — essentially letting the test-taker preview part of the exam. This phenomenon is called data leakage, and it inflates evaluation scores, with the inflated portion coming precisely from memorization rather than generalization. The defense is to split along "the natural boundaries of information flow," not by whichever rows are most convenient to divide. For document tasks, the natural boundary is usually the source document; if revision relationships or template reuse exist between documents, further grouping by "source family" is needed. The author's core criterion is: the splitting unit should reflect how information flows across boundaries, not make the table easiest to divide.

Baseline Stability and What It Actually Measures

The author mentions another independent baseline experiment: comparing a TF-IDF logistic regression baseline against a small PyTorch model on a fixed document split. Labels came from a lexical rubric, not from independently observed results.

After adding five random seeds on the same fixed split, the baseline's test macro-F1 stabilized at approximately 0.902; the neural model's range was roughly 0.576 to 0.902. This is a valuable diagnostic — the baseline is stable under this setup, while the neural model shows significant sensitivity to initialization and optimization. Reporting only the best neural model run would mask this sensitivity.

But the baseline also shares vocabulary with the labeling rules. A high score may reflect successful reproduction of proxy rules and does not establish the quality of actual runtime decisions. Repeating seeds tests one source of variation; it cannot produce new independent documents, fix a weak target definition, or make an already-examined test set "fresh" again.

More Samples May Introduce a Different Task

The next data issue is semantic compatibility. A larger synthetic corpus used 8 grading criteria with levels from 0 to 4, while the document prototype used 4 dimensions and 4 evidence states. These are two different targets, and simply concatenating rows does not make them equivalent.

The author gives a completely fictional passage to illustrate: "I explored a video editing tool through tutorials and hope to use it in future team projects." A generative grading rubric might assign a low level for "exposure to the tool"; a document rubric might classify the passage as "insufficient evidence of completed editing work." Neither label automatically corresponds to an actionable decision.

The mapping requires explicitly defined, reviewed examples and documentation of the original target. Ambiguous or incompatible cases should remain visible. Score thresholds cannot substitute for the decision of "what this label actually means." A later local experiment by the author preserved the synthetic corpus's own 8-criterion target rather than silently converting it to the earlier 4-state task — this maintained an important boundary: results on the synthetic task remain results on that task.

Unseen Identifiers May Still Contain Familiar Language

Synthetic data makes it easy to construct coverage and contrast samples, but it also makes shortcuts easy to repeat. Two documents can have different identifiers, names, section orders, and subtle wording changes while retaining the same underlying phrase templates. Exact duplicate detection may pass, but training and test samples remain highly similar in language.

In the corpus the author examined, variants reused phrase foundations and added framing. This constitutes grounds for investigating template overlap, not proof that all results are invalid or that all leakage has been eliminated. Stronger evaluation should track template families, check cross-split similarity, and preserve genuinely different evidence expressions, while also checking whether length, section structure, or stylistic cues expose the generated labels.

Template Overlap and Synthetic Data Shortcuts: Synthetic corpora create samples that "look different" by swapping identifiers, names, section orders, and surface wording, but the underlying phrase templates are often preserved. This provides a shortcut for the model: instead of learning the evidence patterns that truly distinguish labels, it memorizes that "a certain type of template phrase usually corresponds to a certain label." Exact duplicate detection (such as hash-based deduplication) cannot find this overlap because it detects character-level identity, while template variants are entirely new at the character level. Identifying this kind of risk requires finer-grained methods than exact matching, such as n-gram overlap, embedding similarity, or template family tracking. The author's attitude is careful and precise: phrase foundation reuse "constitutes grounds for investigating template overlap" but does not equal proof that all results are invalid or that leakage has been eliminated — it is a signal requiring further verification, not an established conclusion.

The Workflow the Evaluation Model Is Meant to Assist

The product-level question is: do model suggestions help reviewers find and evaluate evidence?

The author proposes the next useful comparison: "documents + search" versus "documents + search + model suggestions." This requires independently reviewed references, positive and ambiguous examples, evidence-missing cases, and explicit handling of extraction failures. What gets measured includes missed evidence, misleading suggestions, corrections, abstentions, and review workload.

Model suggestions and retrieved passages should remain separately inspectable — search results do not automatically constitute an explanation of neural output. Reference review should also avoid showing model suggestions first, otherwise the evaluation inherits the model's framing. Disagreements need to be resolved or recorded as pending, not fabricated into a consensus. This research is not yet complete; it is the next piece of evidence needed to judge usefulness, not another interpretation of existing training scores.

Workflow-Level Evaluation: Traditional model evaluation computes classification metrics on a fixed dataset, measuring "how well the model performs on existing labels." Workflow-level evaluation extends the evaluation object to the complete human-machine collaboration process, measuring "whether the reviewer's actual work improves after introducing model suggestions." The key difference lies in what is measured: the former measures label reproduction, the latter measures outcome metrics such as missed evidence, misleading suggestions, correction counts, abstention rates, and review workload. Such evaluations typically require independent human references, explicit failure handling, and a process design that collects reviewer judgments before showing model suggestions, to avoid the evaluation being "anchored" by the model's framing. The author notes this research is not yet complete; it is the next piece of evidence needed to judge usefulness, not another reading of existing training scores.

Questions to Ask Before Comparing Scores

The author summarizes a checklist written before comparing methods:

• What do the reference labels mean? Who or what produced them?
• Which classes and operational failures have actual support?
• What is the independent unit: a row, a document, or a source family?
• Has the evaluation set already influenced design decisions?
• Are the new labels compatible with the existing task?
• Which workflow outcome would justify adding the model?

The number 90% is useful precisely because scrutinizing it changed the next action. The system needs better reference coverage and independent workflow comparisons to support claims about usefulness.