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Design Patterns for Discriminating Tests

Design starts from the prediction

For each test, link:

candidate → mechanism → prediction → observable → operationalization → design → analysis → interpretation

Choose the design that can distinguish candidates under realistic uncertainty. Do not select a design merely because it is familiar or available.

NIH-aligned rigor questions

Where applicable, address:

• rigor of the prior research forming the scientific premise;
• unbiased and well-controlled design;
• relevant biological variables such as sex, age, weight, or health condition;
• authentication and validity of key biological/chemical resources;
• transparent methods, analysis, interpretation, and reporting.

Apply only the elements relevant to the science and explain omissions.

Core design record

Every design should state:

• study system and target population;
• experimental/observational unit and analysis unit;
• sampling frame and recruitment/selection;
• interventions/exposures and comparator versions;
• allocation, randomization, concealment, and masking;
• outcomes, timing, measurement IDs, and quality control;
• positive, negative, vehicle/sham, procedural, or reference controls as applicable;
• inclusion, exclusion, attrition, and stopping;
• sample-size, precision, or information rationale;
• analysis IDs and estimands;
• safety, ethics, feasibility, data, and regulatory gates;
• replication, transport, and external-validation plan.

Experimental designs

Randomized intervention

Useful for causal contrasts when intervention, allocation, and ethics permit.

Check:

• allocation sequence and concealment;
• intervention versions, adherence, contamination, and co-interventions;
• masking of participants, providers, outcome assessors, and analysts where feasible;
• primary estimand and intercurrent events;
• intention-to-treat or other analysis population aligned to the estimand;
• harms, stopping, missing outcomes, and protocol deviations.

Randomization does not solve measurement bias, nonadherence, post-randomization selection, interference, or poor external validity.

Factorial design

Useful for multiple interventions and interactions.

Check:

• scientific meaning and scale of interaction;
• power/precision for interactions, not only main effects;
• compatibility and safety of combined conditions;
• multiplicity and hierarchy;
• whether sparse combinations undermine interpretation.

Within-unit or crossover design

Useful when effects are reversible and carryover can be controlled.

Check:

• period and sequence effects;
• washout rationale;
• time trends and learning;
• missing periods;
• whether the condition is stable and intervention reversible.

Perturbation and rescue

Useful for mechanistic candidates when ethically and technically appropriate.

Check:

• perturbation specificity and off-target effects;
• manipulation check;
• rescue interpretation and overexpression artifacts;
• temporal order;
• orthogonal perturbations and measurements;
• relevant negative and positive controls.

A rescue can still be explained by compensatory or non-specific effects.

Time-course

Useful when candidates predict different ordering or dynamics.

Check:

• sampling times justified by expected process;
• independent versus repeated units;
• baseline and pre-trend;
• measurement stability across time;
• multiple looks and timepoint multiplicity;
• lag, feedback, and reverse causation.

Observational designs

Cross-sectional

Can estimate prevalence and associations at a defined time. It usually cannot establish temporal direction. Explicitly consider selection, reverse causation, survival/prevalence bias, and common-method measurement.

Cohort/longitudinal

Can establish measured temporal ordering and incidence. It does not eliminate confounding.

Check:

• time zero and eligibility;
• exposure updates and time-varying confounding;
• loss to follow-up and informative censoring;
• competing events;
• immortal-time and delayed-entry risks;
• outcome ascertainment changes.

Case-control

Efficient for some rare outcomes.

Check:

• source population and control sampling;
• matching implications;
• exposure measurement and recall;
• selection mechanisms;
• correct effect measure and sampling analysis.

Natural/quasi-experimental

Can strengthen causal identification when an assignment mechanism or discontinuity is credible.

Check:

• assignment mechanism and manipulation;
• continuity, parallel trends, exclusion, or instrument assumptions as applicable;
• anticipation and spillovers;
• bandwidth/window choices;
• placebo/negative-control tests;
• sensitivity to specification and clustering.

The design label alone does not establish identification.

Computational and theoretical designs

Simulation

Use to test implications of assumptions, estimator behavior, or model dynamics.

Record:

• data-generating process and parameter ranges;
• rationale for scenarios;
• seeds and software versions;
• performance targets and uncertainty;
• failure cases and sensitivity;
• separation between simulated truth and empirical validity.

Simulation can show consequences within a model, not that the model describes nature.

Predictive model evaluation

Separate prediction from causation.

Check:

• target population, outcome, time origin, and horizon;
• leakage and preprocessing;
• train/tune/test independence;
• calibration and discrimination;
• uncertainty and subgroup performance;
• temporal/geographic/external validation;
• dataset shift and update policy.

Secondary-data analysis

Record provenance, data-generating process, inclusion, missingness, transformations, version, and prior analysis exposure. Avoid using the same data to generate and confirm a hypothesis without transparent separation or independent validation.

Controls

Positive control

A condition expected to produce a known response. It checks whether the system and measurement can detect a relevant effect.

Procedural control

Matches handling, timing, delivery, or processing without the target active component.

Negative control

Should not operate through the target mechanism but should share relevant bias pathways. State assumptions and failure interpretation.

Null comparator

A comparator representing no intervention or no difference may be useful, but it is not equivalent to a negative control and may not isolate placebo, handling, expectancy, or background trends.

Measurement validity

Before collecting target outcomes:

• define constructs and proxies;
• verify instrument validity in the target context;
• assess reliability/repeatability;
• calibrate and authenticate resources;
• prespecify detection limits and quality failures;
• plan masking and standardized acquisition;
• define missing/invalid values;
• test cross-site, cross-device, cross-group, or longitudinal comparability where relevant.

A precise measure can be precisely wrong. Technical replicates do not replace independent biological, participant, site, or experimental units.

Sample size and precision

Do not use universal minima.

Base planning on:

• primary estimand and effect/precision target;
• expected variability and dependence;
• allocation ratio;
• attrition/missingness;
• multiplicity or sequential design;
• model complexity;
• feasibility and ethical burden;
• uncertainty in planning values.

Report assumptions and sensitivity to them. Pilot data may be too unstable for definitive effect-size planning; use external evidence, conservative ranges, or precision-based goals where appropriate.

Multiplicity

Inventory:

• candidate hypotheses;
• outcomes and timepoints;
• subgroups and interactions;
• model specifications and transformations;
• interim looks and stopping;
• repeated datasets or cohorts.

Prespecify a strategy appropriate to the inferential goal, such as:

• family-wise error control;
• false-discovery-rate control;
• hierarchical/gatekeeping testing;
• multilevel estimation;
• clearly labeled exploratory analysis without confirmatory claims.

Do not report only favorable analyses. Threshold crossing is not a quality score or probability that a candidate is true.

Missing data and deviations

Define:

• missingness by variable, time, and group;
• reasons and data-collection process;
• primary handling;
• assumptions;
• sensitivity analyses;
• protocol and analysis deviations.

Complete-case analysis is not automatically unbiased. Record deviations without overwriting the original plan.

Replication and open materials

Following the National Academies terminology:

• reproducibility uses the same data/code/conditions;
• replicability collects new data to address the same question.

Plan:

• code, environment, seeds, and workflow capture;
• provenance and versioning;
• shareable materials and justified restrictions;
• independent replication;
• boundary-condition and transport tests;
• reporting of null and contrary results.

Open sharing remains subject to consent, privacy, community governance, intellectual property, biosecurity, and other controls.

Intervention reporting

For randomized intervention work:

• use SPIRIT 2025 and its explanation/elaboration for protocol completeness;
• use CONSORT 2025 and its explanation/elaboration for result reporting;
• include trial registration, protocol and statistical-analysis-plan access, outcomes, harms, intervention/comparator details, analysis populations, missing data, and important changes;
• use applicable extensions.

These are reporting guidelines. They do not replace ethics review, trial registration rules, statistical expertise, or regulatory requirements.