17  Preliminary Studies and Pilot Trials

A definitive study is expensive, and it commits you to a stack of assumptions you’d rather not discover are wrong once the money is spent. Some of those assumptions concern the intervention itself: that the problem looks the way you think it does in this setting, that the community will accept the proposed solution, that it’s the right one in the first place. Others concern the machinery of the trial: that the intervention can be delivered as designed, that eligible people will enroll and stay, that the measures will behave the same here as in the study they were borrowed from. Preliminary studies are how you test these assumptions while the stakes are still low, rather than after they’re written into a multi-year grant. This chapter is about what preliminary studies can tell us, what they can’t, and how to design them well.

17.1 Types of Preliminary Studies

Preliminary studies is the umbrella term for the full range of early-phase research often conducted before a larger study: qualitative formative research, feasibility and acceptability studies, and pilot trials. The term signals that these studies come before something else: a full-scale trial, a scaled-up program, or a decision to commit money and years to a course of action.

A good preliminary study replaces assumptions with data from the setting. It surfaces implementation problems while you can still fix them: revise the protocol, retrain staff, redesign the technology, or rethink the intervention itself. It also sets the success criteria that make a later go/no-go decision principled rather than improvised. It is judged by whether you learned what you needed to learn, not by whether it produced a statistically significant effect (Platt et al., 2022). Each type answers a different question, as Table 17.1 shows.

Table 17.1: Types of preliminary studies and the questions they answer
Study type Core question
Formative qualitative study What does this condition mean to people here, and what should the intervention look like? Includes user-centered design and cultural adaptation work.
Feasibility and acceptability study Will the intended recipients accept and use the intervention, and can it be delivered as designed (staffing, materials, supporting technology) in field conditions? Records actual use as well as stated intent.
Pilot trial Do the full trial’s procedures work: randomization, blinding (if applicable), delivery, outcome assessment? Internal pilots are embedded in the main trial; external pilots precede it.

Terminology varies. In the framework Eldridge and colleagues developed for studies that prepare for a randomized trial, feasibility study is the umbrella term, and pilot studies are the subset that run part or all of the future trial on a smaller scale (M. Eldridge Sandra et al., 2016). This chapter uses preliminary studies as the umbrella so it can also include formative work done before any particular trial is planned.

The three types often run as a development pathway, in the order this section follows: formative qualitative research to understand the context, a feasibility and acceptability study to check that people accept and use the intervention and that procedures work, and a pilot trial to run the full study’s procedures at small scale. Some programs move through all three; others combine them or run only the ones their uncertainties demand. The labels describe a study’s main purpose, not a strict boundary.

FORMATIVE QUALITATIVE RESEARCH

Formative qualitative research is usually the first step, whether a team is building an intervention or bringing one into a new setting. Through in-depth interviews, focus groups, and observation—the methods of Chapter 13—it asks questions that quantitative approaches usually can’t answer: What does this health condition mean to people here? How do they understand its causes and remedies? What would make them more or less likely to take part, and what concerns do they have that researchers haven’t anticipated? The answers shape your approach, how you describe the intervention to potential participants, which outcomes you measure, and how you train the staff who deliver it.

Designing a New Intervention

Sometimes no existing intervention fits the problem, and a team has to start from scratch. The conventional approach asks people to describe their experience and needs, then leaves the design work to professionals.

User-centered design, also called human-centered design or design thinking, brings the intended users into the design process itself, using techniques borrowed from product design.

User-centered design typically moves through a sequence: understand the people and the context, generate candidate solutions with them, build rough prototypes, and test those prototypes with users before committing to a design. Early prototypes are expected to fail, and each round of user feedback reshapes what gets built next. What distinguishes the approach is who gives the feedback: the people generating ideas and testing prototypes come from the population the intervention is meant for. Co-design can show that a design fits and that its users want it. It can’t show that the intervention can be delivered at scale or that it works.

Prototype testing is where usability gets assessed: can people manage what the intervention requires, such as completing the steps, navigating the app, or following the protocol, without excessive effort? Usability is a separate question from whether people like the design. A participant can find an app appealing and still get lost in its menus, and only watching real users attempt real tasks will reveal it.

A team in two districts of Oromia, Ethiopia, used this approach to design ways to increase antenatal care visits and births in health facilities (Lakew et al., 2026). Its first round held separate workshops with pregnant women and with husbands, partly so that providers wouldn’t overshadow their views. Later workshops with health workers and community influencers built on what the women and husbands had said. In all, 204 people took part in the workshops and prototype testing.

One of the teams’ rough prototypes, couples listening together to recorded stories about pregnancy and birth on simple radio devices, became a self-paced audio program recorded in Afan Oromo, with illustrated print materials for people who can’t read.

The prototypes were tested twice: first with 24 members of the design teams, who checked that their ideas had made it in, then with 36 people in six focus groups who hadn’t helped design them. The first round prompted a guide for the women who would deliver the program, and the second prompted revisions to the stories, to fit local culture and language, and new discussion questions for couples to use after listening.

Adapting an Existing Intervention

Building on an intervention that already has evidence behind it is often more efficient than developing a new one, which matters when health systems are stretched and research funding is scarce (Moore et al., 2021; Ould Brahim et al., 2025). Adaptation is the deliberate modification of an intervention to improve its fit and acceptability in a new context, such as a different country or population. A team can change the content, the dose or intensity, who delivers it (peers instead of nurses, say), the format (an app instead of in-person sessions), or the procedures, such as where and when it happens.

Every change carries a risk. Fidelity is the degree to which an intervention is delivered as designed and keeps its core components, the active ingredients linked to how it works and responsible for its effects. A change that alters a core component can dilute the intervention’s effect or even cause harm nobody anticipated. Too little change and people may reject the intervention; too much and it may stop working. Adaptation frameworks manage this tension by setting out a systematic process for making an intervention fit while limiting the changes that would weaken it.

One recent framework, the Consolidated Approach to Intervention Adaptation (CLARION), draws on the Medical Research Council’s guidance for complex interventions, an earlier method for adapting programs through community engagement, and a scoping review of the steps that existing adaptation frameworks have in common (Ould Brahim et al., 2025). It has two phases. The first, initial adaptation, has six steps:

  1. Assemble a steering committee of people who know the population, the settings, and the intervention: patients and caregivers, health workers, and researchers, including the intervention’s developers where appropriate.
  2. Select a candidate intervention, usually through a review of the literature, confirming that it has evidence behind it and that nothing already available meets the need.
  3. Identify its mechanisms of action and core components, from theory, published evidence, and the developers, so the team knows what it shouldn’t change.
  4. Try the unadapted intervention with members of the target population and the health workers who serve them.
  5. Identify and consolidate potential modifications from what those users report.
  6. Have the steering committee adjudicate each proposed modification against criteria agreed in advance.

The first phase produces a preliminary version of the adapted intervention. In the second, interest holders give feedback on that version, and the steering committee decides on any further changes. The output is the version to be pilot tested, which is where the rest of this chapter picks up.

NoteCultural Adaptation

Global health research often carries an intervention from the setting where it was developed, frequently a high-income country, into a very different one. Cultural adaptation is the form of adaptation this calls for. It goes beyond translation to ask how the intervention’s core mechanisms interact with local beliefs, values, and practices. That makes two of CLARION’s steps harder. The people advising on the adaptation need to include people from the culture, and the core components themselves may not travel. When group interpersonal psychotherapy was adapted for depression in rural southwest Uganda, the trainee group leaders, who had grown up in the study districts, didn’t recognize loneliness as a trigger of depression in communities where people took part in communal life every day; in their view, isolation could be the result of depression rather than its trigger (Verdeli et al., 2003). A review of cultural adaptation models found agreement on five stages: information gathering, preliminary design, preliminary testing, refinement, and a final trial. The same review noted that few studies had directly compared an original intervention with its culturally adapted version (Barrera et al., 2013).

FEASIBILITY AND ACCEPTABILITY STUDIES

Once an intervention has been designed or adapted, the next step is to try it with the people and in the settings it’s meant for. Studies at this stage usually ask two questions together: do people accept the intervention and want to use it (acceptability), and can it be delivered as designed in real conditions (feasibility)?

Bowen and colleagues treat acceptability as one dimension of feasibility rather than a separate category (Bowen et al., 2009), and that’s the spirit here.

Acceptability

Acceptability asks whether people want or would use an intervention. Sometimes that means testing an idea or prototype before it exists in full: would participants find this approach appropriate, and would they engage with it? Other times it means putting a working version in front of people and gauging their reaction to the real thing.

It’s hard for people to react to something they’ve never seen. People say “sure, I’d use that,” and once the intervention is built, fewer of them use it than said they would. Ideation and co-design are still useful, but what people say about a hypothetical is weaker evidence than what they do with something real. Either way the questions are similar: Do they find the approach culturally appropriate and aligned with their values? What concerns do they have, and what modifications would address them?

When you ask about acceptability, ask about its parts separately: whether people understand what the intervention involves and why it might help (cognitive acceptability), how they feel about taking part and whether emotional barriers exist (affective acceptability), how likely they are to engage with each component (behavioral intentions), whether the intervention fits local beliefs, values, and practices (cultural alignment), and whether the time and effort it asks for seem reasonable (perceived burden).

To interpret acceptability data, you need to understand why people say they’ll do something and then don’t. Social desirability leads participants to express enthusiasm they don’t feel, particularly when researchers are perceived as authority figures. What seems acceptable in an interview may prove unacceptable when it competes with real-world demands. People also underestimate how burdensome future commitments will feel: “attending weekly sessions” sounds manageable in the abstract and becomes difficult when specific weeks arrive. And circumstances change: an intervention that was acceptable at enrollment may become unacceptable when family obligations shift or health status changes.

Feasibility

Feasibility studies ask a practical question about the intervention: can it be delivered as designed? Can staff deliver it with adequate fidelity? Do the supporting systems and technology function in field conditions? What are the real costs in time, money, and personnel? Some feasibility studies also check recruitment and follow-up, but testing the trial’s procedures, randomization included, is the main purpose of a pilot trial, taken up below.

Set success criteria before you collect data, because a threshold chosen afterward tends to fit whatever you found. Table 17.2 lists the domains a feasibility study usually covers, with the form a benchmark for each might take. Notice that the acceptability benchmark counts what people do, such as refusals and dropouts, rather than how satisfied they say they are.

Table 17.2: Domains a feasibility study tests, the question each answers, and an illustrative benchmark. The numbers show the form a benchmark takes; they are not recommended thresholds.
Domain Question Example benchmark, set in advance
Engagement Do people use the intervention once it exists? At least 70% attend four of five sessions
Fidelity Can staff deliver it as designed? Supervisors rate at least 80% of observed sessions as adherent to the manual
Delivery resources Do staff time, supplies, and costs fit what the program can sustain? Sessions run within the 90 minutes budgeted, and no site runs out of materials
Acceptability Do participants and providers find it appropriate and manageable? Few refusals or dropouts attributed to the intervention, and no barrier raised in interviews that would stop delivery

A positive feasibility result at small scale doesn’t guarantee feasibility at large scale. Research staff running a 30-participant study, with researchers watching closely, may reach fidelity that routine staff can’t sustain in a 500-participant trial, where supervision is spread thinner and sites vary more. Researcher attention, resources, and participant motivation may all be higher in preliminary work than in routine implementation.

Feasibility and Acceptability in Practice

A pilot of the Learn, Engage, Act, Dedicate (LEAD) intervention in Kenya used both records and interviews to assess feasibility and acceptability (Giusto et al., 2022). LEAD is a five-session intervention for fathers with problem drinking that combines behavioral activation, motivational interviewing, and strategies for discussing masculinity, delivered by lay counselors in a peri-urban community near Eldoret. Nine fathers took part. Community leaders and counselor trainees referred them, and each had an AUDIT score indicating problem drinking without likely dependence, a child aged 8 to 17, and a partner willing to report on his behavior.

Acceptability checks started before any father enrolled. Psychology graduates of Moi University in Eldoret reviewed the draft manual and took structured notes on its feasibility, acceptability, understandability, and cultural relevance, and every session was role-played to test its flow and language. The team then examined session transcripts and selected supervision records from the first two participants before finalizing the manual.

For feasibility, the team relied on records. Supervisors kept attendance logs from counselors’ post-session forms, with a rule for what counted as missed: a scheduled session skipped without 24 hours’ notice. Session length came from the audio recordings, cross-checked against the times counselors wrote in their notes. These records showed that eight of the nine fathers completed every session and that sessions averaged 91 minutes against a design of 60 to 90. The three counselors had been selected from six trainees on their training performance, including a rating of their counseling skills.

For acceptability, research assistants who weren’t involved in delivering LEAD interviewed each father individually, in Kiswahili, for about an hour. That separation can reduce the pressure on fathers to praise the counselors who treated them. The interviews asked about the content, the materials, the counselor, and how helpful LEAD had been, and two coders analyzed the transcripts with a shared codebook. The team also checked what fathers said against what they did: almost all of them called the notebook and activity schedules useful, and their high rates of completing homework and remembering their notebooks backed that up.

The one father who stopped attending was interviewed too, to learn why. He lived near an “alcohol den,” a home that produces local brew. His son’s circumcision, an occasion for heavy drinking, fell during treatment, and his wife may have been ambivalent about the treatment. He had asked for home sessions to avoid travel, which the authors read as a possible sign of low motivation. Asked directly, he said he stopped because he lacked time. The authors identified three candidate barriers a next study could assess or address early in treatment: partner ambivalence about the treatment, proximity to alcohol, and initial motivation to engage. None of them would show up in an attendance rate.

The interviews also left a gap. Fathers said little about the masculinity discussions, so the study produced little evidence on whether that component was acceptable. Interviews need to probe each component, not only the intervention as a whole.

PILOT TRIALS

Pilot trials run the full trial’s procedures at small scale: recruitment, randomization, blinding if the design needs it, follow-up, and measurement. Table 17.3 gives the question each answers and the form a benchmark might take. A pilot trial also checks delivery fidelity, the same question a feasibility study asks, now under trial conditions.

Table 17.3: Domains a pilot trial tests, the question each answers, and an illustrative benchmark. As in Table 17.2, the numbers show the form a benchmark takes, not recommended thresholds.
Domain Question Example benchmark, set in advance
Recruitment Can we identify, screen, and enroll eligible people at the rate the timeline assumes? At least half of eligible people approached consent, and each site enrolls eight a month
Randomization and blinding Do staff follow the allocation procedure, do participants accept it, and does blinding hold? Staff follow the allocation procedure for every participant, few participants decline because of random assignment, and no allocation is inadvertently disclosed to blinded outcome assessors
Follow-up Can participants be reached for follow-up, and how many are lost? At least 80% complete the final assessment
Measurement Do assessors administer the measures as designed, and do the data come back complete? Fewer than 5% of items missing, and the assessment takes under 45 minutes

Internal or External Pilots

The core decision is whether the pilot is part of the main trial or a separate study before it. An internal pilot is the first phase of the main trial, and its participants usually stay in the final analysis. An external pilot is completed before the main trial begins, and its participants aren’t part of the main trial’s analysis.

The choice turns on how much might need to change. Use an internal pilot when the design is settled and the remaining uncertainty is about recruitment, retention, or the parameters behind the sample size calculation. Wittes and Brittain proposed the design so a trial could re-estimate parameters such as the outcome’s variance or the control-arm event rate, and increase its target if the original assumptions proved too optimistic (Wittes et al., 1990). By the time an internal pilot runs, though, the protocol is fixed and participants are enrolling, so it can’t pre-test the feasibility or acceptability of the larger study (Platt et al., 2022). It allows operational adjustments, such as a more flexible dosing schedule, but changing the intervention or the outcomes may mean the pilot’s data can’t be included in the main analysis (Avery et al., 2017).

Use an external pilot when the intervention, the outcomes, or the trial procedures might still need substantial change. The same goes for deep uncertainty about recruitment: when no one can say how many eligible people there are, the UK’s National Institute for Health Research (now the National Institute for Health and Care Research) recommended that researchers consider an external pilot rather than an internal one (Avery et al., 2017). The cost is time and money: an external pilot is a separate study, often with its own funding and ethics review, and the main trial can’t start until it ends.

Both kinds can carry progression criteria, benchmarks set in advance and used to judge whether and how the main trial goes ahead (Avery et al., 2017; S. M. Eldridge, Chan, et al., 2016). Recruitment is the most common focus, and protocol adherence and outcome data are the other usual concerns (Avery et al., 2017).

Underpowered by Design

A pilot trial is sized to test whether the trial’s procedures work, not whether the intervention works. Almost every pilot is therefore underpowered to detect an effect, and that’s by design.

This rules out a tempting move. If the pilot happens to produce a statistically significant effect, the team declares that the intervention works. If it doesn’t, the team says the pilot was too small to tell. Under that logic the pilot can’t fail, so it was never a test. The CONSORT extension for pilot trials advises against framing a pilot around hypothesis tests of effectiveness (S. M. Eldridge, Chan, et al., 2016), and the Duke guide says a pilot protocol shouldn’t propose inferential tests at all (Platt et al., 2022).

Analyze a pilot descriptively instead. Report each process measure, such as recruitment or retention, against the benchmark set for it in advance. Report any outcome data as estimates with confidence intervals. The intervals will be wide, which is an accurate picture of what a small sample can tell you. Recruitment, retention, and other process estimates can inform the next trial’s design. A preliminary treatment-effect estimate is usually too imprecise to determine the main trial’s sample size (Leon et al., 2011).

Multiple Sites

Many full trials run at several sites. A single clinic or district rarely has enough eligible people to reach the sample a trial needs in reasonable time, and a result from one site says little about whether the intervention works elsewhere. Spreading a trial across sites in different health systems or communities addresses both problems, but it adds ways for the trial to fail that a single-site pilot can’t reveal. If the uncertainty concerns coordination across sites or differences in how sites recruit and deliver the intervention, the pilot needs more than one site. A single-site pilot can still answer narrower questions about procedures.

The pilot sites should represent the range of conditions the full trial will meet, not only the best ones, because recruitment at the team’s home site or at the most enthusiastic centers may overstate what the others will achieve (Avery et al., 2017). Coordination is part of what gets tested, since communication and data procedures that work for two sites can break down at ten. So is consistency: whether training reaches every site in the same form, whether local adjustments erode fidelity, and whether data quality differs systematically between sites. Expect procedures to perform differently across cultural and linguistic groups, even within a single country.

Pilot Trials in Practice

A randomized feasibility trial of diabetic foot-care education in Ghana shows the questions a pilot trial can answer, and how a pilot that meets every target can still change the main trial (Suglo et al., 2024). People with diabetes at risk of foot ulcers attended four weekly group sessions with a family caregiver, led by nurses at the diabetes clinic of a teaching hospital in Kumasi. Fifty pairs were randomized, 25 to the program and 25 to usual care.

Can the trial recruit and keep enough participants? Yes, by the progression criteria the team set in advance (Table 17.4). The authors report that every criterion was met.

Table 17.4: Progression criteria in the Ghana foot-care feasibility trial. Each pair was a person with diabetes and a family caregiver. The interest target comes from the trial protocol; the others are the paper’s predefined progression criteria. Data from Suglo et al. (2024).
Criterion Target Result
Interest At least 350 pairs express interest within six months 434
Consent At least half of eligible pairs consent and are randomized 50 of 83 (60%)
Loss to follow-up No more than 30% of pairs lost 10 of 50 (20%)
Retention At least 70% of participants assessed at 12 weeks 77 of 100 (77%)
Data completeness 12-week data complete for at least 70% of participants 70 of 77 returned questionnaires (91%)
Attendance A mean of at least three of the four sessions 3.84

Where is the recruitment bottleneck? The authors point to eligibility. Of the 434 people who expressed interest, only 83 were eligible, and 60% of the exclusions came from the requirement that a family member take part too. None of the criteria set in advance tracked this; the authors added the measure after the study started. The authors suggest letting people enroll without a caregiver at the clinic and passing the information to the family by phone, video, or print.

Does randomization work in this setting? It met its progression criteria, but the authors report two problems. Enthusiasm for the program made the control arm unattractive, and several interested people declined for that reason. Two blood relatives with diabetes were randomized to different arms, and there was some sharing of intervention materials between participants. The authors suggest that a waiting-list design or a stepped-wedge cluster design, in which everyone eventually receives the program, might be more acceptable and could increase recruitment.

Are the outcome measures and follow-up adequate for a main trial? The authors concluded that both need work. The questionnaires were well completed, but none had been developed and validated in sub-Saharan Africa, so the authors say their cultural relevance should be confirmed before further trial use. They also note that observing ulcers or amputations would have needed at least 6 to 12 months of follow-up, not 12 weeks.

Does the program work? The authors note that the trial wasn’t designed or powered to show an effect. Its efficacy signals favored the program on every questionnaire, in an analysis of the participants still in the study at 12 weeks, but the authors caution that these signals have wide confidence intervals and should be interpreted with caution.

17.2 Designing Preliminary Studies

A poorly designed preliminary study wastes money, can leave the team falsely confident or falsely discouraged, and leaves the uncertainties that prompted it unresolved.

START WITH CLEAR AIMS

Before designing anything, write down what you want to learn. A pilot added to a protocol without stated questions can’t tell you whether it succeeded. The questions worth asking are the ones whose answers would change the next study: whether the intervention needs revising, whether recruitment can reach its target, whether participants will stay through follow-up. For each one, note the evidence that would answer it and what you would do with the answer. The domains in Table 17.2 and Table 17.3 are the usual candidates, but rank them rather than trying to test them all at once.

Take one question from a pilot of a five-session counseling program: will participants attend? The measure is the share who complete all five sessions, taken from attendance logs with a written rule for what counts as a missed session. A benchmark of 70% might rest on what the main trial needs, since below that too few participants would receive enough of the program for the trial to test it fairly. If attendance falls short, the team uses exit interviews to learn why before deciding whether to change the schedule, the venue, or the counselors’ training.

A study focused on acceptability might rely on qualitative data, and one focused on recruitment on counts and rates. Measure what your aims require, and resist adding “one more measure” to a protocol that’s already long.

FRAMEWORKS FOR PRELIMINARY STUDY DESIGN

Several frameworks exist, but the one to know is the CONSORT extension for randomized pilot and feasibility trials (S. M. Eldridge, Chan, et al., 2016). It’s a reporting guideline, but it works as a design tool because it lists what a well-run pilot should be able to report. It asks for feasibility objectives rather than efficacy hypotheses. It asks for prespecified criteria for deciding whether to proceed, where they apply, and suggests that in many pilots they are best viewed as guidelines rather than strict thresholds. And it asks for participant flow from screening through follow-up, and for a statement of how the findings will inform the decision to proceed. If you can’t state your success criteria before data collection begins, the design isn’t finished.

For the intervention itself, you already have a framework: the logic model you built for measurement planning in Chapter 9. Each box in the model is an assumption a preliminary study can test: inputs arrive, staff deliver the activities, participants show up and engage. Recall the Healthy Activity Program example (Section 9.2.2), where lay counselors deliver six to eight weekly psychotherapy sessions under structured supervision. The feasibility benchmarks come straight off the diagram: counselors trained, sessions delivered at the intended length, attendance, fidelity. Preliminary work tests the left side of the logic model (inputs, activities, outputs) so the main trial can ask whether the outcomes on the right side follow.

Theory of Change approaches help identify what needs to be true for an intervention to work before you test whether it works.

CHOOSING THE SAMPLE SIZE

Size a preliminary study for the uncertainty it has to resolve. Of the three buckets in Chapter 16, a preliminary study draws on the first two, saturation and precision. It doesn’t need the third, a power calculation for the intervention’s effect, because its aims are preliminary: it isn’t sized to show that the intervention works.

When the job is to explore, as in formative qualitative work, saturation applies: keep collecting data until new interviews stop adding information that bears on the question. When the job is to see whether procedures hold up in the field, the study needs enough participants for the problems to show. The LEAD pilot in Kenya enrolled nine fathers, enough to measure attendance, session length, and acceptability (Giusto et al., 2022). Nine is too few to pin down a recruitment rate, though.

When the job is to estimate a number the main trial depends on, such as a dropout rate, precision applies. Decide how precisely you need to know it, then size the study to get there. The Duke guide works an example: to estimate dropout of about 20% to within 10 percentage points at 90% confidence, it puts the requirement at 52 participants (Platt et al., 2022), somewhat more than the roughly 44 that the simple margin-of-error formula gives.

Cluster trials need particular care. Decide which quantities a cluster pilot can estimate usefully and which will also need evidence from other studies (S. M. Eldridge, Costelloe, et al., 2016).

When an external pilot’s job is to estimate a continuous outcome’s standard deviation, Whitehead and colleagues recommend 75, 25, 15, and 10 participants per arm. Those figures are for main trials powered at 90% to detect extra-small, small, medium, and large standardized effects, and they assume the main trial’s sample size will be calculated with the noncentral-t method of Julious and Owen, which allows for uncertainty in the pilot’s standard deviation (Whitehead et al., 2016). The authors chose them to minimize the total number of participants across the pilot and the main trial. Smaller effects need bigger main trials, where an error in the standard deviation costs more participants, so a bigger pilot pays for itself. The rule assumes the main trial keeps the pilot’s design and outcome, so it fits pilots whose procedures are already settled.

PLANNING FOR REVISION

Expect to change your intervention, procedures, and measures based on what you find, and build time for revision into the schedule before the main trial begins.

A pilot of a multi-component intervention for women after fistula surgery in Uganda enrolled 12 women (Barageine et al., 2024). All 12 rated each component very useful, and they found the questionnaires and interviews manageable. The burden was in the intervention itself: some women said fewer sessions would be easier, and the authors wrote that the results suggested modifications to the protocol to reduce participant burden. Involve your implementation partners in interpreting findings like these and planning the changes, since the people who will deliver the intervention often know things the researchers don’t.

Revision takes time. Protocol revisions may require new materials, retraining, and another test of the modified procedures, so schedule those tasks before committing to a start date for the main trial.

BUDGETING FOR PRELIMINARY RESEARCH

Preliminary studies cost money and staff time, and they need their own budget lines. When they’re squeezed into unfunded time between other projects, corners get cut, and the main trial pays for what was skipped.

Personnel time is usually the largest category: principal investigator time for design, oversight, and interpretation; research coordinator time for protocol development and implementation; data collection staff; data management and analysis support; and community engagement personnel. A pilot in northern Tanzania, in which a community health worker delivered hypertension education to adults in HIV care, began with two weeks of training for that one worker (Manavalan et al., 2022). The trainer’s time and the worker’s time both belong in the budget.

Direct costs include participant compensation set for the local context, travel to field sites, supplies and materials, technology, venues, and laboratory or clinical assessments. Preliminary studies also often reveal the need for infrastructure (training materials, data systems, quality assurance procedures) that the larger trial will use but that has to be paid for up front.

When money is tight, as it is for most global health research programs, four strategies help. Pilot first the uncertainties that would most change the main trial, rather than piloting everything at once. Nest preliminary work within existing studies where possible. A pilot of electronic consent procedures in Malawi ran as a sub-study of an ongoing controlled human infection study, testing a new procedure on participants who were already enrolled (Ngoliwa et al., 2024). Nesting saves time and money, but it has limits: participants completed paper consent before e-consent, and the authors agreed that this familiarity may explain why e-consent produced no errors. Use existing research infrastructure: established relationships with clinical sites, trained data collectors from other projects, shared data systems. And understand your funder’s expectations, since some funders explicitly support preliminary work while others expect it to be completed before the main proposal.

17.3 Communities, Ethics, and Capacity

Preliminary research is often a community’s first contact with a research program. If community members experience it as extractive (researchers arrive, collect data, and leave), that impression can shape how they see the program for years. If community input shapes the research questions and procedures, later studies start with a working relationship.

BUILDING THE MODEL WITH STAKEHOLDERS

For complex, systems-level interventions, build the theory of change with the stakeholders who will make the intervention run. A participatory theory of change draws on what they know about the system (Seward et al., 2021). The Mental Health in Primary Care (MeHPriC) initiative in Lagos, Nigeria, which integrated mental health services into primary care, co-created its theory of change over 18 months in 2013 and 2014 with more than 150 participants from government, health facilities, and communities (Adewuya et al., 2025). A workshop, 36 stakeholder consultations, and technical working groups in 2013 produced the first map of causal pathways, assumptions, and indicators before services launched in January 2014, and the authors report that the process secured buy-in. Two later workshops refined the map using data from the implementation itself.

Partnership starts before the study does, by asking community stakeholders which questions matter most to them, since their priorities may differ from the researchers’. Tell communities what the preliminary data show as you learn it, rather than waiting for the final paper. When community members raise concerns about research procedures, change the protocol where you can. And from the beginning, ask what happens after the research ends: which elements of the intervention community organizations could sustain, and what resources will remain.

WHEN THE PROCEDURE IS THE PROBLEM

In interviews with clinicians recruiting for a suicide-prevention trial in Pakistan, standard consent procedures, built on individual autonomy, clashed with shared, family-based decision-making (Memon et al., 2024). And in rural Pakistan, local health officials sometimes escort investigators for safety, and the presence of an official the participants know, or of police, can influence the consent process (Fazal, 2022).

A team facing concerns like these can modify the procedure, for instance with an alternative consent process that doesn’t require a signature. It can do more community engagement to understand and address the underlying fears. Or it can accept that the research may not be appropriate for this community yet. Proceeding anyway, with the concerns ignored, isn’t an option, because part of a preliminary study’s job is to find out whether the research is appropriate. Sometimes the answer is “not yet” or “not like this,” an outcome the go/no-go decision has to allow for.

ETHICAL OBLIGATIONS

Starting a full trial while major uncertainties about local delivery and participation remain unresolved can waste participants’ time, put their wellbeing at risk, and spend money that could have gone elsewhere. That is an ethical reason to do preliminary research. Preliminary studies also need the same ethical review as any other research with human participants; calling a study “preliminary” doesn’t reduce the oversight it needs.

Early-phase work adds three obligations, and each follows from the fact that its participants mostly help someone else. They may complete long assessments, sit for several interviews, and give feedback on procedures that will benefit future participants more than themselves, so ask only what your aims require. They should also understand what they’re part of: the development of a study, not a proven intervention. That matters most where participants have limited access to healthcare, so say plainly what the study does and doesn’t offer. Finally, decide in the protocol, not when participants ask, what they’ll receive: whether they’ll get the intervention if the full trial shows it works, and what services or referrals are available in the meantime.

BUILDING RESEARCH CAPACITY

When an international team has more research capacity than its local partners, preliminary research can widen that gap or narrow it. In a preliminary study, local researchers can serve as co-investigators who shape the questions and the analysis. Local institutions can help design the study as well as run it. Findings can go to local audiences as well as international journals, and data sharing agreements can let local researchers use the preliminary data for their own work. Training local researchers and building skills in community organizations belong in the plan from the start.

17.4 From Preliminary Findings to the Main Trial

WHAT TO USE FROM THE PILOT

A useful preliminary study ends with a list of specific changes to the protocol, like the Ghana trial’s. Evidence that staff struggled to deliver the intervention with fidelity, or that participants found the procedures burdensome, matters at least as much for the next trial as any number the pilot produces.

The pilot also supplies local estimates for the main trial’s sample size calculation (Chapter 16). Each comes from a small sample, so use it with its uncertainty:

  • Standard deviations and attrition. Plan from the cautious end of the confidence interval. If a pilot observes 20% dropout with a 90% confidence interval of 10% to 30%, assume 30% (Platt et al., 2022). For a standard deviation, inflate the pilot’s estimate to allow for its imprecision, for example by using an upper confidence limit (Whitehead et al., 2016). An attrition rate from a shorter follow-up than the main trial’s will understate dropout.
  • Recruitment. Budget for the low end of the yield. LEAD enrolled 9 of 27 nominated fathers, one in three (Giusto et al., 2022), but the 95% confidence interval (Wilson score) runs from 19% to 52%.
  • ICCs. A pilot rarely has enough clusters to estimate an intraclass correlation precisely, and Eldridge and colleagues advise against planning from its upper limit, which could produce a considerably overpowered trial. Read it alongside published ICCs from similar settings (S. M. Eldridge, Costelloe, et al., 2016).
  • Effect sizes. Don’t plan from them. A small sample makes the estimate too imprecise (Leon et al., 2011), and when power is low, statistically significant estimates tend to exaggerate the effect’s magnitude and can sometimes point in the wrong direction (Gelman et al., 2014). If only promising pilots go forward, the trials that follow are planned from inflated effects and end up underpowered (Kraemer et al., 2006). Plan instead from the smallest effect that would matter to patients or the health system.

Every estimate also reflects the pilot’s conditions. Close supervision can keep attrition lower and delivery more consistent than routine staff will manage, and an estimate from one or two sites may not hold across a main trial’s sites. Treat pilot estimates as one input alongside published estimates from similar settings.

THE GO/NO-GO DECISION

The decision to move from preliminary work to a full trial should rest mainly on process criteria, because those are what a preliminary study is sized to measure. Did recruitment reach its target rate? Was retention high enough to give you sufficient follow-up data? Could staff deliver the intervention as designed? Did participants and staff find the procedures manageable? Did the measures work, with acceptable levels of missing data and no comprehension problems?

Avery and colleagues suggest a traffic-light system rather than a simple stop or go (Avery et al., 2017). Green means continue: there are no concerning issues. Amber means amend: there are problems that can be remedied, and the trial proceeds with caution once they are. Red means stop: the problems can’t be remedied. The line between amber and red is whether a problem can be fixed, not how large it is; Avery and colleagues place a severe but temporary drop in recruitment, such as one caused by a trial manager’s sickness absence, in amber. For an amber result, ask how much the unmet benchmarks matter, whether protocol changes can fix them, and whether more preliminary work would resolve what’s left.

Treat the benchmarks as guidelines rather than strict thresholds, as the CONSORT extension suggests for many pilots (S. M. Eldridge, Chan, et al., 2016). LEAD enrolled nine fathers against a target sample of ten (Giusto et al., 2022). For planning the next trial, enrolling only nine of 27 nominated fathers matters more than falling one participant short of the target. A criterion set in advance doesn’t make the decision for you, but it lets readers see how you made it. When a result misses a benchmark, say so, and explain why you’re proceeding, amending, or stopping.

Safety and community concerns can change the decision even when every process benchmark is met. A pilot is too small to show that an intervention is safe (Leon et al., 2011), but a serious, unexpected harm is grounds to stop or amend, and some trials write safety into their progression criteria (Avery et al., 2017). Whatever you decide, report the problems the preliminary work revealed, and either fix them or proceed knowing the risk.

DOCUMENTATION AND REPORTING

The CONSORT extension for pilot and feasibility trials lists what to report (S. M. Eldridge, Chan, et al., 2016). A useful report also describes the specific challenges that emerged and how the team handled them, not only whether benchmarks were met. It records what participants, staff, and implementation partners observed about feasibility and acceptability, how the protocol changed during the study and why, and what changes the findings point to for the main trial. Other researchers can use a well-documented preliminary study even if your own trial never happens.

17.5 Closing Reflection

Each preliminary study in this chapter tested assumptions its team would otherwise have carried into a full trial. In Uganda, the trainee group leaders didn’t recognize loneliness as a cause of depression in their communities, which called one of the intervention’s problem areas into question. LEAD showed how to look at feasibility and acceptability: records of what fathers did, interviews by people who hadn’t delivered the sessions, and the two checked against each other. The Ghana foot-care trial met every progression criterion and still found that its eligibility rules excluded most of the people who wanted to take part.

What a preliminary study hands the main trial is a list of changes and a few local estimates, such as attrition and recruitment yield, to be used at their cautious end. The treatment effect has to wait for the trial itself. Recruitment, retention, fidelity, and the logistics of delivery can be tested at small scale, while changing the protocol is still cheap.

Those tests only help if the study is designed to answer specific questions, with success criteria set before data collection and time left to act on the results. The preliminary phase is also usually where a team’s relationship with a community begins, and where it learns whether the research belongs in that setting at all.

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