percom-experiments

name	percom-experiments
description	Use when designing or auditing IEEE PerCom empirical evaluations, covering real human subjects, leave-one-subject-out / cross-subject evaluation, F1 and event-level metrics on imbalanced activity classes, deployment realism (free-living vs. lab), fair baselines, contamination-aware model ablations, and matching evidence to the shape of each pervasive-computing claim.

PerCom Experiments

Use this before submission when the evaluation is not yet locked. PerCom reviewers are ubicomp empiricists; the evaluation is where a sensing idea is won or lost, and — because the review is a single round with a bounded rebuttal — the evaluation must be complete at submission (you cannot add experiments in the rebuttal). The organizing principle is evidence proportional to the claim, tested on people and conditions a skeptic would accept.

Evaluation audit

• Evaluate cross-subject by default. A recognition claim about users needs leave-one-subject-out (or leave-one-session-out) results, not a pooled split that lets the same person appear in train and test. Within-subject numbers are a supporting detail, never the headline.
• Use real human subjects, described by count and relevant characteristics, with the collection protocol stated. Report how many, doing what, wearing/placed where.
• Report the right metric. Human activity is imbalanced (most of a day is "null"), so F1 (macro and per-class), precision/recall, or event-level metrics tell the truth where raw accuracy flatters. Say whether metrics are frame-level or event-level.
• Test deployment realism. Distinguish lab vs. free-living and scripted vs. spontaneous behavior; a result only shown on scripted in-lab data invites the "does this survive daily life?" objection.
• Choose fair baselines, including the strongest prior method and a simple-but-reasonable alternative, tuned with a documented, equal budget. An untuned baseline is a scored weakness.
• Report variance: confidence intervals across subjects/folds, number of runs, and the source of stochasticity. Per-subject distributions matter more than a single mean here.
• Design limitations in, not on: know before you collect which generalization and construct limits the study will have (subject diversity, ground-truth quality), and instrument to bound them.

Claim-to-evidence design table

Ubicomp claim	Matching evidence	Reject pattern avoided
"Recognizes activity for new users"	Leave-one-subject-out F1 with per-subject spread	"Within-subject / pooled split inflates the number"
"Works in daily life"	Free-living data, event-level metrics	"Only scripted in-lab sessions tested"
"Beats the prior recognizer"	Same data + tuned baseline, equal budget	"Baseline untuned or on a different split"
"Handles class imbalance"	Macro-F1 + per-class recall, stated balance	"Raw accuracy hides the rare-class collapse"
"The model adds the value"	Ablation vs. classical features/heuristics	"Model's marginal contribution never isolated"
"Generalizes across contexts"	Diverse subjects/environments + explicit limits	"One population, claimed universal"

Contamination- and leakage-aware evaluation

Sensing pipelines leak in subtle ways; the reviewer's first questions are about splits and leakage:

[Subject leakage]  never let one participant appear in both train and test -- LOSO prevents it
[Session/time leak] windows from one recording session can leak across a naive random split
[Normalization leak] fit scalers/PCA on train only; a global normalization leaks test statistics
[Pretraining]      if a foundation model is used, report whether test subjects/data could be in its
                   training set; prefer held-out or post-cutoff data
[Ablation]         isolate the model's marginal value against a classical-feature baseline

Human-subjects provenance floor

• State subject count and relevant demographics, the collection protocol, and IRB/consent status.
• Pin device models, firmware, sampling rates, and sensor placement; archive the extracted, de-identified dataset, not just a description.
• Report the labeling protocol, who labeled, and inter-annotator agreement — silent label noise skews every downstream number.

Vignette: evaluating a HAR recognizer

Suppose the paper claims a wearable recognizer beats a prior model on daily activities. The matching plan: collect from a diverse participant set over multiple days of free-living; evaluate leave-one-subject-out; report macro-F1 and per-class recall with confidence intervals across subjects; run both models on the same folds with an equal, documented tuning budget; add an ablation against classical features; and state external validity (population, device) as a bounded limitation — every number traceable to a logged run in the artifact, because the rebuttal cannot add a run.

Reporting floor

• Cross-subject metric (F1/event-level) with confidence intervals and per-subject spread for the headline comparison; say what the intervals represent.
• Number of runs and the source of variance for any stochastic component.
• The compute actually consumed, not vague feasibility language.

Output format

[Evaluation readiness] strong / adequate / weak (remember: no new experiments in the rebuttal)
[Claim -> evidence map] <claim: subjects / split (LOSO?) / metric (F1?) / setting (free-living?)>
[Baseline fairness] <baseline -> tuned? equal budget? same split? documented?>
[Leakage check] <subject / session / normalization / pretraining leakage handled? yes/no>
[Limitations-by-design] <generalization/construct limit -> instrumentation to bound it>
[Decision-critical run to finish before submission] <one experiment>