Free scoping read. A written assessment of your manuscript in two business days, at no cost.

Start one

Home›Services›Research services›Experimental Design Service

Study Design and Protocol Development

Experimental Design Services

Pubrica’s subject matter experts and statisticians design studies for academic researchers, pharmaceutical and biotechnology companies, CROs, medical device manufacturers and public health teams. We deliver the design rationale, sample size calculation, randomisation plan, protocol and ethics package, all settled before data collection, because a study design cannot be corrected once the data exist.

  • Question, hypothesis and variables defined so that the analysis follows from them
  • The appropriate design selected: randomised controlled, factorial, crossover, quasi-experimental or observational
  • Randomisation, blinding and controls specified in enough detail to be implemented
  • Sample size with the assumptions stated, with the feasibility check that many calculations omit
  • Protocol, ethics submission and registration, with an independent design review before you commit
Design at a glance · one completed project Cluster-randomised · CONSORT

Design selected from the study constraintsCluster RCT

Sample size with the design effect applied+58% for ICC

Randomisation and blinding specified in fullConcealed

Outcomes operationalised with validated instruments4 defined

Protocol written to the reporting guidelineSPIRIT, CONSORT

Question → design → sample size → protocol → ethics → recruitment

Included in every design
  • Chosen from constraints
  • Bias addressed by design
  • Sample size calculated
  • Written to a guideline
  • Ethics-ready
5,000+Experimental research designs built
Since 2009Supporting researchers through publication
ICH-GCPCONSORT, SPIRIT, STROBE, ARRIVE
ISO 9001:2015Quality management certified · cert. H3CR9TCU20251212INDQM10N

Service Scope

Six Experimental Design Service Areas, Available Individually

Our experimental design services are offered separately, so you can engage us at any stage, from an initial research question to a protocol returned by an ethics committee.

Question, hypothesis and variables The research problem refined into something answerable, the gap established against the published literature, and the hypothesis written so it can be tested rather than merely supported. Then independent, dependent and control variables defined and operationalised — which is where most vague studies become specific, because a variable you cannot describe measuring is a variable you have not defined.
Methodology development The design selected from your constraints and built to address the threats it exposes you to — internal validity first, meaning selection bias, confounding, measurement bias, attrition and regression to the mean, and then external validity, meaning whether the result will hold outside the population and setting you studied. Every design trades one against the other, and the trade should be deliberate.
Randomisation, blinding and control The randomisation method chosen for your sample size — simple randomisation leaves real imbalance below a hundred participants, so blocked, stratified or minimised allocation is usually the answer — with the sequence generated independently and concealed until the moment of allocation. Blinding specified for participants, clinicians, outcome assessors and analysts separately, because they can be blinded to different degrees and usually are.
Sample size and the statistical plan Power analysis with the effect size argued as clinically meaningful rather than chosen because it is achievable, inflated for the design effect where clusters are randomised and for realistic attrition. Then the analysis plan itself: the model, the covariates, the handling of missing data, the pre-specified subgroups and the multiplicity strategy, all written before any data exists.
Protocol, ethics and registration The full protocol written to SPIRIT or the template your sponsor uses, with the informed consent documents, the participant information sheet, the data management plan and the ethics committee submission. Trial registration before the first participant is enrolled, on the registry your region and your target journals require.
Independent design review A second opinion on a design somebody else built — yours, a collaborator's, or one a CRO has proposed. A written critique of the threats it leaves open, whether the sample size supports the claim, what a reviewer or a regulator will challenge, and what can still be changed. Commissioned most often after an ethics committee or a funding panel has raised a methodological question.

Types of Study Design

Fifteen Study Designs and Their Applications

Across biomedical sciences, health policy and public health — true experimental, quasi-experimental and observational.

Randomised controlled trialThe design that minimises bias and confounding by allocating at random, for therapeutic, preventive, diagnostic and screening interventions. Phase I, Phase II and Phase III protocols, with the design requirements that differ between them built in rather than inherited.
Crossover designEach participant receives both conditions in a randomised order, so the comparison is within the person. A large efficiency gain, available only where the condition is stable and the treatment effect reverses.
Cluster-randomised trialClinics, wards, practices or communities randomised rather than individuals, because that is how the intervention is delivered — with the design effect applied to the sample size rather than discovered at review.
Stepped-wedge designEvery cluster crosses to the intervention in a randomised order until all have it. Frequently the only design an ethics committee will approve for something that cannot be withheld.
Factorial designTwo or more interventions tested simultaneously by randomising each question independently. Two answers for close to the cost of one, provided the interventions do not interact — and that assumption has to be stated.
Solomon four-group designAdds unpretested groups to a pretest-posttest design so that the effect of the pretest itself can be separated from the effect of the intervention. Rare, expensive and the correct answer when testing changes behaviour.
Pretest-posttest control group designThe most widely used design in applied and educational research: both groups are measured before and after, with the control group showing what would have happened without the intervention. Baseline measurement also allows adjustment for chance imbalance.
Post-test-only control group designRandomisation without a pretest, used where measuring beforehand would itself change behaviour or where a baseline is impossible. Simpler, and it gives up the ability to check baseline balance.
Single-subject and N-of-1 designsOne participant randomised repeatedly between conditions across periods. Answers what works for this patient, which is the right question in rare disease and in personalised treatment decisions.
Adaptive designsPre-specified rules that allow sample size re-estimation, arm dropping or seamless phase transitions as data accumulate. Efficient but demanding: every adaptation must be specified in advance, with the type I error controlled across the whole design.
Pragmatic and registry-based trialsRandomisation embedded in routine care, using registries or health records for outcomes. Far cheaper per participant and far more generalisable, at the cost of less control over what happens between randomisation and outcome.
Sequential designsInterim analyses with pre-specified stopping boundaries for benefit, harm or futility, so a trial can end as soon as the answer is clear rather than when recruitment finishes.
Blinded and double-blind trialsBlinding specified separately for participants, treating clinicians, outcome assessors and analysts, with the placebo or sham designed to be genuinely indistinguishable — and the success of blinding tested rather than assumed.
Quasi-experimental designsFor when randomisation is impractical, premature or ethically impossible: interrupted time series, difference-in-differences, regression discontinuity and non-equivalent control groups. Weaker by design, and far stronger than the before-and-after study they usually replace.
Descriptive and observational designsCohort, case-control and cross-sectional studies that identify patterns, trends and outcomes without manipulating anything — designed against confounding and selection, and reported under STROBE.

Research Areas We Cover

Designs are developed by specialists who know the field they are for, across oncology, cardiology, neurology and psychiatry, infectious disease and vaccines, endocrinology, respiratory medicine, surgery, rare disease, medical devices and diagnostics, nutrition and dietetics, public health and epidemiology, health policy and services research, education and behavioural science, and preclinical and in vivo work reported under ARRIVE. Where a question spans fields, such as a behavioural intervention with a biochemical endpoint or a device trial with a patient-reported outcome, the team includes specialists from each, because a design borrowed from one field may not meet the standards of the other.

Who We Serve

Researchers and Organisations We Support with Experimental Design

We support five main client groups, each of whom needs a study designed to answer its research question before resources are committed.

Academic researchersExperimental design for theses, dissertations and publications — methodologies built for accuracy and reproducibility, and written to the standards an examiner and a journal will apply.
Pharmaceutical and biotechnology companiesProtocol development and design support for pre-clinical work, randomised controlled trials and the phase-specific requirements of Phase I, II and III programmes.
Clinical research organisationsIndependent design review, statistical validation and methodological consultation, providing a second opinion on a design before a sponsor sees it, when changes are still inexpensive.
Medical device manufacturersExperimental and quasi-experimental designs for diagnostic, screening and interventional device studies, built to ISO 14155 and the regulatory expectations that differ from drug trials.
Public health researchersEpidemiological, observational, descriptive and community-based designs structured for scientific accuracy and for policy relevance — which are not always the same requirement.

When to Involve a Methodologist

The best time is before the funding application, when the design can still be shaped around the available budget and the methods section can be written to score well. The second is after a grant is awarded and before recruitment opens, when the design can still be fully revised and when most clients contact us. The third is after an ethics committee, supervisor or reviewer has raised a methodological objection. A review is still worthwhile then, because the objection can often be answered without a redesign. We cannot rescue a study whose participants were recruited under a design that cannot support its claim.

Compliance and Standards

Reporting and Methodological Standards for Study Design

Pubrica works in compliance with the guidance below. Each standard governs a different kind of study, and the right one is chosen at the design stage, because a checklist applied afterwards only shows what should have been done.

ICH-GCPE6(R3)

Good Clinical Practice (ICH-GCP)

The framework for any research involving human participants: protocol content, investigator responsibilities, informed consent, data integrity and the audit trail. It is what an ethics committee and a monitor read your protocol against, and the R3 revision moves it towards a risk-proportionate approach rather than a uniform one.

CONSORT and SPIRIT (trials and trial protocols)

SPIRIT governs the protocol, CONSORT the finished report, and they are deliberately aligned — a protocol written to SPIRIT already contains what CONSORT will ask for. Extensions cover the design you are using: cluster, crossover, stepped-wedge, N-of-1, pilot and feasibility, non-inferiority, and AI-enabled interventions.

STROBEobservational

Strengthening the Reporting of Observational Studies in Epidemiology (STROBE)

For cohort, case-control and cross-sectional studies, where the threats are confounding and selection rather than allocation. Designing to STROBE forces the decisions that matter in observational work — how exposure and outcome are defined, which confounders are measured, and how participants were selected — before the data exists rather than after.

ARRIVEin vivo

Animal Research: Reporting of In Vivo Experiments (ARRIVE 2.0)

For preclinical work, where the reproducibility problem is worst and the remedies are the simplest: randomisation, blinded outcome assessment, a stated sample size with its justification, and pre-specified inclusion and exclusion criteria. Many journals now require the ARRIVE Essential 10 as a submitted item.

ISOWHO · FDA

Device, regulatory and global guidance (ISO 14155, WHO, FDA)

ISO 14155 for clinical investigations of medical devices, alongside FDA guidance on adaptive designs, non-inferiority margins and patient-reported outcomes, and WHO guidance where a study spans countries. Device studies in particular have design requirements that differ from drug trials and are routinely discovered late.

Registration and the ethics committee

A clinical trial must be registered before the first participant is enrolled, on ClinicalTrials.gov, CTRI, ISRCTN or the registry your region requires, as a condition of publication at any ICMJE member journal. Retrospective registration is visible and permanent, and it often leads to rejection at submission. The same protocol serves the ethics committee, and the questions an IRB or IEC asks are predictable: how participants are identified and approached, what consent covers and how it is documented, what happens to people who decline, how risk is minimised and monitored, and what happens to the data afterwards. We write the protocol so that all of these are answered in one document rather than assembled under time pressure after a first rejection.

Responsible Use of AI

Our Approach to AI Use in Experimental Design

Design tools can propose a sample size, randomisation scheme or allocation ratio in seconds. They cannot tell you whether the effect you powered the study to detect is the one worth detecting, which is the question on which the whole design depends.

How We Use AI ToolsCalculating power curves across a range of assumptions, so you can see how sensitive the sample size is; drafting randomisation lists; and checking a protocol against its reporting guideline.
Where We Do Not Use AIWe do not use AI to choose the effect size, primary endpoint or analysis population, to decide what is clinically meaningful, or for any design submitted to an ethics committee or regulator without a named statistician responsible for it.
What Your AI Declaration Should IncludeYour declaration states the tool, the stage at which it was used and the human oversight applied. Journals, funders and the ICMJE January 2026 update now expect this, and an undeclared tool found later is treated as a research integrity matter.

Why We Do Not Publish AI Accuracy Figures

Accuracy figures for AI tools are usually reported by the companies that sell them.

Pubrica therefore does not quote a self-generated accuracy figure, because it would carry the same conflict of interest. Instead, we tell you which tool was used on your project, at which stage, and what a specialist changed afterwards.

Methodology

How Our Experimental Design Process Works

The process has twelve stages, each led by the Pubrica specialist qualified for it: a subject specialist, methodologist, statistician, clinician or regulatory consultant.

Stages one to three

Problem, gap and hypothesis

Subject specialists and methodology experts. The research problem defined and refined so that it is scientifically relevant and genuinely novel; a review of the existing literature to establish the gap, avoid duplicating work published while you were planning, and justify the need; and then the hypothesis or research question itself, written so that it is testable rather than merely interesting.

Stages four and five

Variables and the design

Methodology experts and clinicians. Independent, dependent and control variables defined and operationalised into things that can actually be measured. Then the design type selected — true experimental, quasi-experimental, descriptive, randomised controlled, crossover, factorial — from the constraints rather than from habit, with the protocol aligned to clinical and regulatory expectations.

Stages six and seven

Sample size, randomisation and blinding

Statisticians and clinicians. Power analysis and sample size with the assumptions sourced rather than assumed, inflated for the design effect where clusters are randomised and for realistic attrition. Then the randomisation method — blocked, stratified or minimised — with concealment of allocation specified, and blinding taken as far as the intervention honestly allows.

Stages eight and nine

Measurement and data collection

Subject specialists and regulatory consultants. Instruments chosen because they are validated in your population rather than because they are familiar, with standardisation across sites and assessors. Then the data collection process itself: who records what, when, on which form, with what checks — structured to satisfy ethical and regulatory requirements before the first entry rather than after the first monitoring visit.

Stages ten and eleven

Statistical plan and ethics

Statisticians and regulatory experts. The analytical framework, the models and the tests, written down before any data exists — which is what makes the eventual result pre-specified. Alongside it the ethics and regulatory package: committee submission, informed consent documents, and compliance with ICH-GCP and the standards your study and region require.

Stage twelve

Interpretation, validation and reporting

Subject specialists and methodology experts. Once results exist, findings validated against the plan, placed in the context of the literature the design was built from, and structured for the destination — a manuscript written to CONSORT or STROBE, a thesis chapter, or a funding report. This is also where the honest limitations are written, by the people who know where the design was compromised.

Free Study Design Assessment Before Quotation

Before quoting, a methodologist reviews your question and constraints and tells you which design can answer it, approximately how many participants it will need and what may make it harder. This takes two business days and is free. Occasionally the question needs narrowing before any design will work, and we identify this before any cost is incurred.

What We Need From You
The questionYour hypothesis, or the question behind it
What existsPilot data, prior studies, preliminary work
The scopePopulation, setting, timeframe
The constraintsBudget, recruitment, ethics, equipment
Any preferencesMethods or instruments you intend to use
Any draftAn early design or framework, if you have one

The constraints matter more than the preferences, although researchers usually send the preferences first. Achievable recruitment, previous ethics committee approvals, whether the outcome can be assessed blind and the time available determine the design, so we ask about these first.

Study Design Selection Tool

Selecting a Study Design Based on Research Constraints

Four questions determine most experimental study designs. Answer them to see which design they indicate, its trade-offs and what reviewers are likely to question.

Answer four questions to identify a suitable study design True experimental design

Question one

Is the intervention delivered to individuals, or to whole groups?

A treatment one patient receives is delivered to an individual. Training a clinic, changing a ward protocol or altering a school curriculum reaches everyone in that place at once.

Question two

Can it ethically and practically be withheld from some participants?

A national policy, a mandated guideline or a system that goes live for everyone cannot be withheld. If it can only be delayed rather than withheld, answer no.

Question three

Can one unit receive both conditions, one after the other?

This needs a condition that is chronic and stable and a treatment whose effect wears off. A cure, a surgical procedure or anything with lasting effect rules it out.

Question four

Are you comparing two conditions, or more than two?

Two interventions that act independently can often be tested together rather than sequentially, which is where a factorial design is most useful.

Recommended Design for Your Constraints

Parallel-group randomised trial

True experimental

Two arms, randomised once

BaselineIntervention periodFollow-up
Group A
Group B

No intervention yetInterventionControl

What it isParticipants are randomised once, to intervention or control, and stay there. The comparison is between people.
Trade-offsThis is the default design and the one reviewers question least. Because between-person variation remains in the comparison, it needs more participants than a crossover for the same precision, in exchange for making no assumptions about carry-over.
What reviewers questionWhether randomisation was concealed until allocation, and whether the groups were balanced on prognosis at baseline. An imbalance in a randomised trial is chance; an imbalance a reviewer can explain by the allocation method is not.
What it requiresAllocation concealment, blinding where it is possible, a pre-registered primary outcome, and CONSORT reporting with a flow diagram that reconciles.

Also worth considering

This tool applies the rules a methodologist uses in an initial consultation. It does not replace that consultation. A complete design must also account for what your ethics committee will accept, how quickly you can recruit, what the funder will pay for, whether the outcome can be blinded and which comparator the field accepts, and these questions require a methodologist’s review.

Why Design Review Before Recruitment Matters

Most elements of a study can be revisited: the analysis can be re-run, the manuscript rewritten, the figures rebuilt and the journal changed. The design cannot. Once participants are recruited, the study can only answer what its design allows. A crossover chosen where the treatment has a lasting effect, a cluster trial analysed as though patients were randomised individually, or a before-and-after study that cannot separate the intervention from the underlying trend is identified at peer review but cannot be corrected at that stage. A consultation with a methodologist before recruitment is the point at which these problems can be avoided at no cost.

Our Experts

Your Experimental Design Team

A named team of subject specialists stays with your project from scoping to delivery. Your project coordinator introduces each member before work begins, and the handover records which of them completed each stage.

Subject matter expertClinical or scientific expert matched to your topic

Reviews the scientific content for accuracy and confirms that each conclusion is supported by the evidence. Each expert is matched to your field of research.

Responsible forScientific accuracy and interpretation
Reviews againstThe study protocol and current literature
FieldMatched to your topic
BiostatisticianStatistical input where the work reports analysed data

Checks that statistical methods, tables and conclusions are consistent with the analysis plan and that the analysis can be reproduced.

Responsible forStatistical accuracy
Reviews againstICH E9 and the statistical analysis plan
ToolsR, SAS, Stata, Python
Data specialistData handling, cleaning and documentation

Prepares, cleans and documents the data so that every step from raw data to final output can be traced and reproduced.

Responsible forData handling and documentation
Reviews againstThe data management plan and applicable data standards
OutputDocumented, reproducible datasets
Second reviewerIndependent check of code and outputs

Independently checks code, tables and outputs against the analysis plan. Discrepancies are logged and resolved before delivery.

Responsible forIndependent quality control
Reviews againstThe analysis plan and outputs
Signed off byProject lead

Sample Work

Sample Experimental Design Handover

Every Pubrica design includes the reasoning as well as the documents: why the design was chosen, what it gives up and what reviewers are likely to question. Use the tabs to view each part.

Experimental design handover

Cluster-randomised trial · 48 clinics · SPIRIT protocol

Design rationale · sample size with design effect · randomisation plan · ethics package

1The deciding constraintThe intervention is a change to how a clinic triages, so it reaches every patient in that clinic. Randomising patients was not possible; randomising clinics was. That single fact selected the design before anything else was considered.
2Why not a stepped wedgeConsidered, because it would have given every clinic the intervention eventually and was likely to be easier with the participating trust. Rejected because the rollout would have run across a winter, and the outcome is strongly seasonal — time and treatment would have been confounded in exactly the way the design is vulnerable to.
3Why not a crossoverA clinic cannot un-learn a triage protocol. The effect does not reverse, so the washout that a crossover depends on does not exist.
4What the design gives upStatistical efficiency: 48 clinics carry considerably less information than 896 independently randomised patients would, which is why the sample is almost 60% larger. The protocol states this rather than leaving a reviewer to point it out.
5Recorded for the ethics committeeCluster allocation means individual patients cannot consent to their arm. The consent model — clinic-level opt-in with individual consent for data collection — was agreed with the committee in advance, which is what avoided a second submission.

Every design considered, and why it was not chosenWritten before recruitment

Redacted extract · client and setting details changedPage 1 of 4

The handover is the protocol and the reasoning behind it. Use the tabs to view each part.

The design rationale is the document researchers often do not know to request and reviewers expect. It records every design that was considered and why it was rejected, so that when a reviewer asks why you did not run a stepped wedge, the answer is already documented and dated before recruitment.

The threats section separates what the design solves from what it can only declare. Contamination between clinics could not be designed out of this study, and stating this in the protocol prevents it from being presented later as an unexpected finding.

Design selected from constraintsWith the rejected alternatives recorded and reasoned.
Sample size calculated and justifiedControl rate sourced, design effect applied, sensitivity run.
Threats addressed or declaredEvery threat is addressed or declared in the protocol.
Ethics package prepared with the protocolThe protocol, the consent documents and the registration together.

Request sample work and we will send a handover based on a study like yours, with the same design, field and regulatory setting.

Experimental design handover · redacted sample

Cluster-randomised trial · 48 clinics · SPIRIT protocol

Design rationale · sample size with the design effect applied · randomisation and blinding plan · ethics package. Client, setting and clinical details have been removed or changed. Ask us and we will send one built around a study like yours.

1Design rationale

The document researchers often do not know to request and reviewers expect. It records every design considered and why it was rejected, dated before recruitment, so that when a reviewer asks why you did not run a stepped wedge, the answer already exists in your own documentation.

DesignVerdict, and why
Individually randomised trialNot possible. The intervention is a change to how a clinic triages, so it reaches every patient in that clinic. This single fact selected the unit of randomisation before anything else was considered.
Stepped-wedge cluster trialConsidered seriously, because every clinic would eventually receive the intervention and the participating trust would have found it easier to agree to. Rejected because the rollout would have run across a winter and the outcome is strongly seasonal — time and treatment would have been confounded in exactly the way the design is vulnerable to.
Cluster crossoverRejected. A clinic cannot un-learn a triage protocol; the effect does not reverse, so the washout a crossover depends on does not exist.
Before-and-after at each clinicRejected. No concurrent control, so any change in referral patterns over the study year would be indistinguishable from the intervention.
Parallel cluster-randomised trialChosen. Concurrent control, no confounding with season, and a unit of randomisation that matches how the intervention is delivered.

What the design gives up, stated in the protocol. Statistical efficiency. Forty-eight clinics carry considerably less information than 896 independently randomised patients would, which is why the sample is almost sixty per cent larger. Saying so in the protocol is better than leaving a reviewer to point it out.

2Sample size

ElementValue and source
Primary outcomeProportion triaged correctly within four hours, at twelve months
Control rate64%, from a twelve-month audit across nine of the participating clinics
Target difference10 percentage points, agreed with the clinical group as the smallest worth changing practice for
Power and alpha90%, two-sided 5%
If randomised individually448 per arm
Design effect1 + (30 − 1) × 0.02 = 1.58, ICC taken from two published cluster trials in similar settings
Inflated for clustering708 per arm
Clinics required24 per arm
Clinics recruited50 in total, allowing for two withdrawing entirely
SensitivityRecomputed at ICC 0.04, which would require 33 clinics per arm. Stated in the protocol as the principal risk to power.

The target difference is the number that decides everything else, and it is the one most often chosen backwards from what is affordable. Here it was agreed with the clinical group before the calculation was run, and the agreement is recorded.

3Threats to validity

Separating what the design solves from what it can only declare. A protocol that addresses the first and admits the second is considerably more convincing than one that is silent about both.

Closed by design
  • Identification bias. Patients are identified and consented before their clinic is told its allocation. A clinic that knows its arm can otherwise select who enters the study, and in cluster trials this is the most common fatal flaw.
  • Unblinded outcome assessment. Triage appropriateness is judged from the record by assessors who are not told the clinic’s arm. The clinicians cannot be blinded; the assessors can, and that is the blinding that protects the primary outcome.
  • Chance imbalance. With 24 clusters in each arm, imbalance on clinic size and baseline performance remains likely. Allocation is stratified on both and the analysis adjusts for them, as pre-specified.
Declared as limitations
  • Contamination. Staff move between clinics within the trust, so control clinics may partially adopt the protocol. This biases towards the null and cannot be designed out; it is stated as a limitation and measured through a staff movement log.
  • External validity. All 48 clinics sit in one health system with one records platform. The protocol says so, rather than implying the result will transfer to systems that work differently.

Agreed with the ethics committee in advance. Cluster allocation means individual patients cannot consent to their arm. The consent model — clinic-level opt-in with individual consent for data collection — was settled with the committee before submission, which is what avoided a second round.

4Files Delivered

  • The design rationale, recording every design considered and the reason each was or was not chosen.
  • The full protocol, written to SPIRIT with the CONSORT cluster extension in view.
  • The sample size calculation, its sources, and the sensitivity analysis around the ICC.
  • The randomisation plan: stratified allocation, sequence generation and the concealment procedure.
  • The statistical analysis plan, with the mixed model, covariates, missing data strategy and pre-specified subgroups.
  • The ethics package: committee submission, consent documents and participant information sheets.
  • The trial registry entry, drafted and ready to file before the first participant is enrolled.

Pubrica supports the work; authorship and accountability remain yours. Where a methodologist’s contribution to conception and design meets ICMJE authorship criteria we say so and let you decide. Any AI assistance in drafting is declared.

Prepared by Pubrica. Pubrica is a trading name of Guires®, registered in England, Wales and India.

Download this as a PDF
Before and after · the methods paragraph from an animal study, redactedPreclinical · ARRIVE 2.0

As supplied

Rats were randomly assigned to treatment and control groups (n = 8 per group).

  • “Randomly” with no method. In practice this often means picked out of a cage, which is not randomisation.
  • No allocation concealment and no blinding of outcome assessment — two of the ten essential ARRIVE items.
  • The experimental unit is not stated. If treatment was given in the drinking water, the cage is the unit and n is 2, not 8.
  • No justification for eight, so the study is either underpowered or over-sized and nobody can tell which.

As delivered

Animals were allocated to groups by a computer-generated randomisation list prepared by someone not involved in the experiment, in blocks of four, stratified by cage. Treatment was given by individual gavage, so the animal is the experimental unit. Outcome assessment and analysis were both blinded to allocation. A group size of eight gives 80% power to detect a 1.2 standard-deviation difference at a two-sided 5% level; exclusion criteria were set before the first animal was treated and two exclusions are reported in the flow diagram.

  • The randomisation method exists, and somebody outside the experiment generated it.
  • The experimental unit is named, which decides the whole analysis.
  • Blinding is stated for the two steps where it changes the result.
  • The sample size is justified and the exclusions are reported rather than absorbed.

These changes are design decisions rather than writing improvements, and they had to be made before the first animal was treated. A paragraph like the revised version cannot be written retrospectively, which is why reviewers and ethics committees read it closely.

Benefits

Benefits of Pubrica Experimental Design Services

A study designed to answer its research question, with a methods section justified in writing.

01Bias addressed by designSelection, confounding, measurement and attrition bias are each addressed by a specific design feature: concealed allocation, stratification, blinded outcome assessment and pre-specified handling of loss to follow-up. Built into the design, they add no cost. Left to be argued afterwards, they become limitations that can lead to rejection.
02Demonstrable reproducibility and validityA registered protocol, a pre-specified analysis and operationalised outcomes mean the study can be repeated and the result checked. Reproducibility is determined before recruitment, and careful analysis cannot create it later.
03Efficient use of study resourcesThe right design is often the less expensive one. A crossover can answer in eighty participants what a parallel trial needs three hundred for, and a factorial design answers two questions for little more than the cost of one. Design choice offers the largest single saving in a study budget, and it is available only at the start.
04Credibility with reviewers and committeesEthics committees, funding panels, examiners and methods reviewers all assess whether the design can support the claim it will make. Experience of more than 5,000 designs means we know what each audience asks, and we answer it in the protocol rather than in a response letter.

Packages

Experimental Design Service Packages

Every package is run by a methodologist with a statistician, a clinician and a regulatory consultant drawn in as the design needs them, with a dedicated project coordinator.

Our Experimental Design Methodologists4 named, in house

Dr. Jonathan Williams

Head – Experimental Research Design

Design selection, randomisation and blinding, and the protocol written to SPIRIT 2025.

Dr. Kunal Bhatia

Principal Scientist – Study Design & Methodology

Cluster, crossover, stepped-wedge and adaptive designs, with the trade-off in each one stated rather than assumed.

Dr. Radhika Ganesan

Research Design Strategy Lead

Observational and quasi-experimental designs, with confounding and selection addressed by design rather than by adjustment afterwards.

Prof. Ananya Deshpande

Experimental Methodology Specialist

Preclinical and laboratory design — the controls, replicates and blinding a reviewer checks — with reporting to ARRIVE 2.0.

Our methodologists are named so that you can verify their expertise. A statistician, a clinician and a regulatory consultant join as the design requires, and a second methodologist reviews every design before delivery. We publish names rather than stock photographs, and the degrees, registrations and publication records of each person are available on request.

Basic

Objective, design and sample size

Academic researchers starting a small-scale or pilot study, who need the shape settled before committing

From $420one primary outcome · one comparison

Delivery 5–7 working days

  • ✓Study objective and hypothesis formulation
  • ✓Selection of the appropriate design, with the alternatives recorded
  • ✓Sample size estimation with its assumptions stated

Add later: randomisation plan; full protocol; ethics package.

View a sample Select Basic
Standard

Design, randomisation and analysis plan

Clinical and biomedical projects of moderate complexity, heading for publication

From $780one study · randomisation schedule and analysis plan

Delivery 7–10 working days

  • ✓Everything in Basic
  • ✓Randomisation and blinding plan, with allocation concealment specified
  • ✓Variable definitions and control group construction
  • ✓Preliminary statistical analysis plan

Add later: full protocol; instrument validation; regulatory check.

View a sample Select Standard
Comprehensive

Full protocol and regulatory readiness

Large-scale trials, multi-centre studies and anything going to a regulator or an ethics committee

From $1,650one trial · full protocol written to SPIRIT

Delivery 10–15 working days

  • ✓Everything in Standard
  • ✓Full protocol development, written to SPIRIT
  • ✓Power analysis and advanced sample size, including design effects
  • ✓Measurement instrument selection and a validation plan
  • ✓Compliance check against ICH-GCP, CONSORT and the guideline your design needs

Add later: ethics submission support; trial registration; SAP in full.

View a sample Select Comprehensive
Custom

Tailored and hybrid designs

Complex, interdisciplinary or high-impact studies, and anything that does not fit a standard design

$150 an hourbilled in half-hours · no minimum block

Delivery By project scope

  • ✓Design built from your goals rather than adapted from a template
  • ✓Hybrid and unusual methodologies, with their statistical consequences worked through
  • ✓Ongoing consultation through recruitment and analysis

Adaptive, seamless, platform, basket and N-of-1 series sit here.

View a sample Select Custom

An independent review of a design prepared by another team is quoted separately and is usually our fastest service. It provides a written critique of what the design leaves open, whether the sample size supports the claim and what a reviewer or committee will question. It is often commissioned when an ethics committee or funding panel has raised a methodological concern that needs a prompt answer.

Quality Assurance

Our Service Commitments and Limitations

A study design determines what a study can find, not what it will find. Our service terms are set out below, before you commit.

Our revision commitment

Revision Support Within the Agreed Scope

We do not offer refunds, because a refund does not get your protocol approved; it ends the engagement with the problem unresolved. Instead, we continue revising the work within the agreed scope.

01

Unlimited revisions within the agreed scope

There is no limit on revision rounds or time within the agreed scope. When ethics committees return comments, supervisors request changes or funders ask for a different comparator, we revise the design.

02

Corrections at Our Cost

If the protocol is returned because of an error in what we specified, such as an incorrect sample size calculation, an omitted design effect or a missed guideline, we correct it at no cost.

03

Delivery on the agreed date

Committee deadlines and funding calls are fixed, and we work to them. If a date is at risk, we tell you early rather than on the day.

04

Final decisions remain with you

We advise on the design, give our view and tell you clearly when we disagree with your preferred approach, but decisions about what is published in your name are always yours.

05

Mutual NDA on request

Signed in both directions before you send anything, at no cost. Your question, your data and our working relationship remain confidential, and we are happy to sign your NDA instead of ours.

9.4/10

Average client rating

From 3,000 responses to Pubrica’s own post-delivery survey, sent to every client at handover between January 2024 and June 2026. This figure comes from our own records.

Service limitations. We cannot guarantee ethics approval, funding or publication, because those decisions rest with committees, funding panels and editors. We also cannot design a study to answer a question that your resources cannot support. Where achievable recruitment will not support the comparison you want, we will tell you and propose a question that can be answered, rather than produce a protocol that appears complete but is underpowered. Where a question cannot be answered as framed, the first deliverable may be a narrower question.

Free methodologist review

Before quoting, a Pubrica methodologist reviews your question and constraints and tells you which designs can answer it and approximately how many participants each would need. Occasionally this review shows that the study as planned cannot work, which is far better to learn at the start than after data collection.

Rejected designs documented

Every design we considered and did not choose is recorded with the reason, dated before recruitment. When a reviewer or examiner asks why you did not run a stepped wedge or a crossover, the answer already exists in your documentation.

GDPR and data privacy

Pubrica works with researchers in India, across the United Kingdom and Europe, in North America, throughout Asia-Pacific and the Middle East, and in Africa and Latin America, and every project is handled the same way wherever it comes from. Your unpublished protocol, your pilot data and your grant application are held under GDPR, kept only as long as the project needs them, never used to train anything, and never shared outside your project team.

No ghost authorship

We design and advise, and we do not act as undeclared authors. Where a methodologist’s contribution to conception and design meets ICMJE authorship criteria, which is common when we built the design, we tell you and you decide, rather than relying on an acknowledgement for a substantial contribution.

Client Stories

Client Feedback on Experimental Design Projects

Testimonials are rephrased from client feedback.

“They took us from hypothesis to data collection strategy without ever letting us skip a step. Working to CONSORT from the design stage rather than at write-up is what made the submission straightforward.”
Samuel — Oncology researcher · USA Published inMDPI Journal—
“Meeting the SPIRIT requirements was the reason we engaged them, but the methodological arguments they raised changed what the study was actually able to contribute.”
Deepa — Public health researcher · USA Published inLancet—
“The protocol had to satisfy both the ethics committee and the methodology, and the detail in the sample size and the randomisation plan is what got us through IRB approval first time.”
Radhika — Clinical researcher · India Published inEuropean Journal of Clinical Nutrition—

FAQs

Experimental Design FAQs

If you need help choosing a design or checking whether your current design will meet reviewer expectations, please ask an expert. No quote is required.

Work from the constraints rather than the preferences. First, establish whether the intervention is delivered to individuals or to whole groups, which decides whether you randomise patients or clinics. Second, establish whether it can be withheld from anyone; if everyone will receive it, a stepped wedge or an interrupted time series is indicated. Third, establish whether one participant can receive both conditions in sequence, which determines whether a crossover is possible. Then consider how many participants you can realistically recruit and what your ethics committee will accept. Once these are answered, the choice between a parallel trial, a crossover, a factorial or a quasi-experimental design is usually clear, which is why the first consultation is short.

Four principles underpin experimental design. Control: something to compare against, so that the effect of the intervention can be separated from what would have happened anyway. Randomisation: allocation by chance, which balances the confounders you know about and, uniquely among methods, the ones you do not. Replication: enough units to distinguish a real effect from noise, which is what a sample size calculation is for. Blocking or stratification: removing a known source of variation from the comparison by design rather than adjusting for it afterwards. Blinding and allocation concealment are then the operational protections that stop these principles being undone in practice — and concealment, which is about the moment of allocation rather than what happens after it, is the one most often confused with blinding and most often missing.

Randomisation. A true experimental design allocates participants or clusters to conditions by chance, which is what allows the groups to be assumed comparable on everything — measured and unmeasured. A quasi-experimental design compares groups that were formed some other way: by policy, by geography, by who volunteered, by what happened before and after a date. That does not make it weak, and the good quasi-experimental designs are considerably stronger than most people assume: interrupted time series, difference-in-differences and regression discontinuity all have ways of ruling out specific alternative explanations. What they cannot do is rule out an unmeasured confounder by design, so the argument has to be made explicitly and defended. Choose one when randomisation is impractical, premature or ethically impossible — and say which of those three it was.

When the condition is chronic and stable, the treatment effect is reversible, and the outcome can be measured more than once. All three conditions hold less often than researchers hope, and if any one fails, a crossover design cannot be used. A cure, a surgical procedure, a vaccine or anything that changes behaviour permanently cannot be crossed over. Where the conditions hold, the efficiency gain is the largest available in trial design: each participant serves as their own control, between-person variation leaves the comparison, and the trial commonly needs a quarter to a half of the participants. The cost is carry-over: if the first treatment is still acting in the second period, the estimate is biased, so the washout must be justified from how the treatment clears rather than from what fits the schedule.

From four things: the outcome's baseline value, the difference worth detecting, the power you want and the significance level you will test at. The arithmetic is the easy part and the assumptions are where studies go wrong. The three most common errors are using an effect size chosen because it makes the study affordable rather than because it is clinically meaningful; taking a control rate from a different population without saying so; and forgetting to inflate. Inflation matters twice over — for attrition, and for clustering. A cluster-randomised trial needs its sample multiplied by the design effect, which with thirty participants per cluster and a modest ICC of 0.02 is a fifty-eight per cent increase. That single omission has under-powered more cluster trials than any other mistake, and it is invisible until the analysis.

Rarely simple randomisation, which is what most people mean by the word. Tossing a coin for each participant leaves real imbalance at realistic sample sizes — with sixty participants, a split as uneven as 38:22 turns up more often than researchers expect. Blocked randomisation keeps the arms level throughout recruitment; stratified blocking does the same within important prognostic groups; minimisation allocates each participant to whichever arm keeps the overall balance best and is the strongest option for small trials with several important factors. Whichever you choose, the part that actually protects the study is concealment: the sequence generated by someone not recruiting, and the next allocation unknowable until the participant is irreversibly enrolled. A perfect sequence that a recruiting clinician can see is not randomisation.

Seven, in roughly this order of frequency. A sample size chosen from what is affordable and justified afterwards. No control group where one was possible. Outcomes defined loosely enough that several measures could be reported and the best one chosen. Clustering ignored in the design and again in the analysis. Allocation not concealed, so recruiters could anticipate the next arm. Attrition unplanned for, with no strategy for the people who leave. And a primary outcome that was changed between protocol and paper — which registries now make visible and reviewers now check. Six of the seven are decided before the first participant, and the seventh is decided by whether the first six were written down.

If it is a clinical trial, yes, and before the first participant is enrolled. Every ICMJE member journal requires prospective registration as a condition of considering the paper, and registering afterwards is permanently visible in the record — the registry shows the date. Use ClinicalTrials.gov, CTRI in India, ISRCTN, the EU CTIS or whichever registry your region and your funder require. Beyond trials, registration is becoming expected more broadly: PROSPERO for systematic reviews, and the Open Science Framework for observational and preclinical protocols, where pre-registration is increasingly what separates a confirmatory finding from an exploratory one in a reviewer's mind. Registration costs nothing and takes an afternoon once the protocol exists, which is the argument for writing the protocol properly first.

Yes, and how much depends on where you are. Before recruitment opens, almost everything is still changeable and a protocol amendment is routine. During recruitment, the design is fixed but the analysis plan, the handling of missing data and the reporting can still be settled properly — and writing them down mid-recruitment is far better than writing them after the data is visible. After the data is collected, we can advise on what the study can honestly support, which is sometimes less than was hoped, and on how to report that without overstating it. The one thing that cannot be done is change what a completed design is capable of answering. If you suspect the design is wrong, the time to ask is now rather than at write-up, when the options narrow to reporting it accurately.

Mostly by making the reporting match the design, which sounds trivial and is where most manuscripts lose credibility. The specific failures are consistent: causal language used for an observational design; a secondary outcome reported as though it were the primary; subgroup findings presented without the interaction test; clustering analysed as though participants were independent; and a limitations paragraph that lists generic caveats rather than the actual weaknesses of this design. Someone who built the design knows exactly where it was compromised and can write those limitations honestly — which reviewers reward, because a paper that names its own weaknesses is far more convincing than one a reviewer has to find them in. The whole thing is then written to CONSORT, STROBE or ARRIVE, with the checklist completed item by item rather than ticked.

A pilot tests feasibility: whether you can recruit, whether the measurement works, whether the protocol survives contact with a real site. It is not powered to estimate an effect, and using its effect size to power the main study is one of the most common and most costly errors in research planning — small samples produce wildly variable estimates, and the ones that look promising enough to justify a trial are disproportionately the ones that overshot. Use the pilot for the variance and the recruitment rate, and take the effect worth detecting from what would change practice or from a published, adequately powered source.

By recognising it in the design rather than patching it in the analysis. If the intervention is delivered to a group, the group is the experimental unit, and analysing individuals as though they were independent inflates the apparent sample size and produces confidence intervals that are far too narrow. The design needs an intracluster correlation coefficient and a design effect, which in a cluster-randomised trial routinely doubles or triples the number of participants required. Getting this wrong is not a subtle statistical point; it is the difference between a study that can answer the question and one that cannot, and it is visible to any reviewer who counts the clusters.

A factorial design tests two or more interventions in the same participants, so that with four arms you answer two questions for roughly the cost of one. It is efficient when the interventions are expected to act independently, and each main effect is estimated on the full sample. It stops being efficient the moment you need to detect the interaction between them, because powering for an interaction typically needs around four times the sample of a main effect. So the practical rule is: use it when you genuinely expect no interaction and would be content to report the main effects, and be explicit in the protocol that the study is not powered to detect one.

What you are trying to show, which changes the analysis, the sample size and the conclusion you are allowed to draw. A superiority trial asks whether the new treatment is better; failing to show it is not evidence that the treatments are the same. A non-inferiority trial asks whether the new one is not worse by more than a pre-specified margin, and that margin is a clinical judgement made and justified before the trial, not a statistical convenience chosen afterwards. Equivalence bounds the difference in both directions. The commonest error is running a superiority trial, finding p > 0.05 and concluding equivalence, which the design does not support.

Not by regulation in most jurisdictions, and increasingly by expectation. A growing number of journals ask whether an observational study was registered and, if it was not, treat the analysis as exploratory — which is a materially weaker claim. Registration on ClinicalTrials.gov, OSF or a comparable platform costs little and does one valuable thing: it establishes that the primary outcome and the analysis plan existed before the data were examined. That is the single defence against the accusation reviewers cannot otherwise rule out, which is that the reported comparison was the one that worked. We register at protocol stage where you want it, and we say in the paper when registration came after data collection.

Request a Free Methodological Review of Your Research Question

We will tell you which designs can answer your question, approximately how many participants each would need and what in your constraints may make it harder, within two business days, at no cost and with no obligation. Before recruitment is the only point at which these decisions can be changed at no cost.

Guides and articles in this section

Show all 1
Get a free quote

Regulations

Check your project against this rule

  1. 1Your work
  2. 2Your details
  3. 3Send
What do you need?

Material you send is held under signed confidentiality, with access limited to the assigned team and encrypted transfer. It is not used to train anything and is not passed to third-party tools. Ask for the agreement before you send anything you would rather cover first.