15 Sampling and Participant Recruitment
The Demographic and Health Surveys have measured health and population indicators in over 90 countries since 1984 (DHS, n.d.). They use rigorous multistage probability sampling—randomly selecting clusters of households, then randomly selecting households within clusters so that results can represent entire national populations. And they’re remarkably good at it. In an evaluation of 14 national surveys, household response rates were 93% or higher, and interview response rates for women ranged from 90% to 98% (Mishra et al., 2008). These numbers reflect decades of investment in sampling frames, interviewer training, community engagement, field logistics, and quality control. The DHS program has turned nationally representative sampling in low- and middle-income countries into something close to routine.
The gap between your intended sample and your actual sample always matters. How large it is, whether it’s systematic, and whether you’re honest about it determine what your findings can and cannot say.
Most research teams will never achieve DHS-level response rates. You won’t have hundreds of trained interviewers, months of fieldwork, or an organization with 40 years of experience navigating community entry in dozens of countries. You’ll have a smaller team, a tighter budget, and a target population that may not want to talk to you. The road will wash out. The gatekeeper will say no. The eligible participant will agree to enroll and then never show up for the baseline survey. The sample you end up with will look different from the one you designed. Sometimes a little different, sometimes dramatically so.
The question is never whether there will be a gap between your intended sample and your actual sample. There always will be. The question is how large that gap is, whether it’s systematic, and what it means for interpreting your results. This chapter covers both sides of the process: how you decide who should be in your study, and the practical work of getting them there.
15.1 Refresher on External Validity
In Chapter 8, we drew a line between two kinds of validity. Internal validity asks whether a causal effect finding is correct for the people you actually studied. External validity asks the next question: does that finding apply to the population or context you care about? Sampling is central to external validity. Who you enroll determines whether your results apply to anyone beyond the participants themselves.
That chapter split external validity into two cases, depending on how your sample relates to your target population:
- Generalizability applies when your sample is a subset of the target population—a trial in Kenyan hospitals meant to inform policy for all Kenyans. The question is whether the people you enrolled represent the broader population they came from.
- Transportability applies when your sample sits outside the target population—applying a trial from India to Kenya, or from urban clinics to rural areas that were never sampled. The question is whether findings cross over to a population the study never touched.
For descriptive estimates like prevalence, representativeness is what matters. If your sample over-represents some groups, your estimate won’t match the population unless you weight it back into shape. For causal effects, the issue is narrower. Populations can differ on countless characteristics without it mattering. What matters is whether they differ on effect modifiers—characteristics for which the treatment works differently. If a drug lowers blood pressure more in younger patients, and your sample skews young, your estimate won’t transport to an older population. If the drug works the same in everyone, the age difference is irrelevant.
Keep this distinction in view as we work through sampling. Most of this chapter is about generalizability: designing a sample that represents the population you want to speak about, and being honest about the gap when it doesn’t. But the deeper lesson from Chapter 8 carries over. A sample doesn’t have to mirror the target population on everything. It has to mirror it on the things that matter for the inference you want to make.
15.2 The Chain of Inference in Sampling
Every study involves a chain of inference with four links:
- Actual sample: Who actually enrolls and completes the study
- Intended sample: Who did you invite to participate?
- Accessible population: Who you can realistically reach?
- Target population: Who you ultimately want findings to apply to
The goal is for your actual sample to represent your target population well enough to support the inferences you want to make. But at each link in the chain, the population can shift in ways that threaten generalizability.
A WORKED EXAMPLE: TUMOR SIZE AND BREAST CANCER SURVIVAL
To see how the chain works, take a concrete question: Is there a relationship between tumor size at diagnosis and breast cancer survival? Trace this question from the target population down to the actual sample, and you can see which links are easy to defend and which are not.
Target Population
Every research question implies a target population. The tumor-size question is about women with breast cancer.
Defining that target population means choosing how broadly to draw the boundary. You could go as wide as all humans, narrow to all women, narrow again to women diagnosed with breast cancer, and narrower still to women diagnosed with breast cancer in a particular region or age range (Figure 15.1). Each level is a legitimate target population. Which one you pick depends on the claim you want to make. For the tumor-size question, a reasonable target is all women diagnosed with breast cancer—the population your finding about tumor size and survival is ultimately meant to describe.
Accessible Population
The target population is who you want to speak about. The accessible population (sometimes called the source population) is the slice of it you can realistically reach, bounded by geography, institutions, budget, and time. You will never have access to every woman diagnosed with breast cancer. What you can reach might be women diagnosed with breast cancer at 10 referral hospitals across 5 countries (still a large study!!). That accessible population is already narrower than the target, and it can differ from it systematically. Referral hospitals tend to see more advanced disease than community clinics, so the women you can reach may have larger tumors and worse survival than women with breast cancer as a whole.
It’s possible that target == accessible populations in some cases. For instance, if you wanted to say something about undergraduate students at a particular university, you could realistically work with the registrar to invite everyone or a random sample of the entire study body. So in that case, you have access to the full target population. Now if you wanted to expand the target population to university students in the country, you’re back to having a gap between your target and accessible populations.
Intended Sample
You probably can’t study everyone in the accessible population either. The intended sample is the set of people you plan to enroll: the women you would draw from those 10 referral hospitals according to your sampling design, whether that’s a random sample, a consecutive series of new diagnoses, or some other scheme. The intended sample is a deliberate selection from the accessible population, and its job is to stand in for that population. How you draw it determines how well it does the job.
Actual Sample
The actual sample is who you end up with: the members of your intended sample who consent, enroll, and contribute usable data. Some women decline. Some are missed. Some enroll but are lost before survival can be recorded. The actual sample is what you analyze, and it drifts from the intended sample whenever non-participation is related to the very things you’re studying—if, say, women with the most advanced tumors are too sick to take part.
Inference Runs the Other Way
A study is designed from the target population down to the actual sample. Inference runs in the opposite direction (Figure 15.2). From your actual subjects you infer to your intended sample, from the intended sample to the accessible population, and from the accessible population back to the target. Each step asks you to assume that the group you have represents the larger group you’re reasoning toward. The steps are not equally safe. The jump from the accessible population (women at 10 referral hospitals in 5 countries) to the target population (all women with breast cancer) is the biggest and the most subjective. It’s the one your sampling design does the least to justify, because no amount of careful sampling within those hospitals tells you whether their patients resemble women treated elsewhere.
TRACING THE CHAIN THROUGH A REAL STUDY
A cross-sectional study of adolescent health in Ethiopia shows how the chain can hold at some links and give way at others (Asari et al., 2026). The research team set out to describe the health issues and needs of adolescents in Ethiopia. They surveyed 722 high-school students in Jimma city, selected by simple random sampling after stratification by sex and grade, and reported on self-rated health, recent health problems, where adolescents look for health information, and whether they can get care.
Start with what they got right, which is most of the lower chain. The accessible population was students at eight of the city’s sixteen high schools, chosen for their socio-demographically diverse student populations. From that population the team drew a probability sample: 737 students selected at random within sex-and-grade strata, sized with a standard formula and deliberately enlarged to represent both public and private schools. Of those 737, 722 took part, a response rate near 98%. The actual sample barely diverges from the intended sample, and the intended sample is a defensible random draw from the accessible population. Well done.
The weakness is at the top of the chain, in the jump from the accessible population to the target. The paper is titled “Health issues and needs among adolescents in Ethiopia,” and its framing implies a national claim. But the accessible population was high-school students in a single city, and nearly four in five came from urban backgrounds in a country that is mostly rural. Out-of-school adolescents were left out entirely. The authors note the exclusion, then minimize it, reasoning that the out-of-school share “might be small, as adolescents are generally in school.” In Ethiopia that assumption is shaky at the secondary level, and the excluded group likely differs on the very things the study measured: access to care, mental health, risky behaviors. No amount of careful random sampling inside Jimma’s high schools can tell you whether those students represent adolescents across Ethiopia.
This is the pattern worth remembering. The team spent its methodological care on the links a probability sample can secure, the random draw and the response rate, and asserted the one link that sampling cannot reach. An inference is only as good as the weakest link in its chain, and here that link is the jump from the accessible population to the target—the one a confident title does nothing to strengthen. More sampling would not fix it. The honest move is a narrower claim: the findings describe urban, in-school adolescents in Jimma, and stand as evidence about Ethiopian adolescents rather than a representative national portrait.
15.3 How Sampling Approaches Vary Across Study Designs
A common mistake in methods sections is treating sampling as if there’s one “correct” approach that applies to all research. There isn’t. The right sampling strategy depends entirely on what kind of study you’re doing and what you’re trying to learn. Let’s walk through four common study designs and see how sampling logic differs for each.
PREVALENCE STUDIES: REPRESENTATIVENESS IS EVERYTHING
When you’re trying to estimate how common something is in a population—say, the prevalence of diabetes in rural Bangladesh or HIV infection rates in Zambia—your sampling strategy must prioritize representativeness. You need every member of the target population to have a known, non-zero chance of being selected. Otherwise, your prevalence estimate will be biased.
This is why large-scale prevalence surveys like the Demographic and Health Surveys (DHS) invest enormous resources in probability sampling. When researchers used DHS data to examine dietary diversity among Ethiopian children, they relied on a multistage cluster design where enumeration areas were selected with probability proportional to size, households were randomly sampled within those areas, and complex survey weights were applied to ensure national representativeness (Seboka et al., 2021).
NoteWhen the Sample Isn’t Representative: Mister P
That rule—known, non-zero selection probabilities—is the design-based path to an unbiased prevalence estimate, and it’s the one to aim for when you can. But it isn’t the only path. Multilevel regression and poststratification (MRP, affectionately “Mister P”) can recover population-level estimates from a sample that was not drawn with known probabilities, including convenience samples, by modeling how the outcome varies across subgroups and reweighting those predictions to match the population’s true composition (Gelman et al., 1997; Park et al., 2004). We work through MRP in Chapter 8, including the famous example of forecasting U.S. elections from a sample of Xbox users (Wang et al., 2015). The method trades a sampling assumption for a modeling one, so the quality of the estimate still depends on how the sample was collected and how well the model and auxiliary data capture the relevant subgroups.
CASE-CONTROL STUDIES: COMPARABILITY OVER REPRESENTATIVENESS
Case-control studies flip the logic. Here, you’re not trying to estimate prevalence—you’re trying to compare people with an outcome (cases) to people without it (controls) to identify risk factors. The sampling priority shifts from representativeness to comparability.
Your controls need to come from the same source population that gave rise to your cases. If your cases are all hospitalized patients, hospital-based controls make sense. If your cases come from a community surveillance system, community-based controls are more appropriate. The key question isn’t “Is this sample representative of the general population?” but rather “Are my cases and controls comparable in all ways except the exposure of interest?”
QUALITATIVE STUDIES: INSIGHT AND VARIATION, NOT NUMBERS
In qualitative research, you’re not trying to estimate population parameters or even achieve representativeness in the statistical sense. You’re trying to gain insight, understand experiences, and capture variation in perspectives.
Purposive sampling is the norm here. You deliberately select participants who can illuminate your research question—whether that means maximum variation sampling to intentionally seek diverse perspectives, key informant sampling to reach people with specialized knowledge, or extreme case sampling to understand what makes unusual or exemplary cases different.
Qualitative researchers often talk about sampling to “saturation,” the point where additional interviews stop yielding new insights.
A study of health research evidence utilization in Tanzania used maximum variation purposive sampling to recruit 52 key informants from national, regional, and council levels of the health system (Kagoma et al., 2024). The goal wasn’t to generalize to all Tanzanian health workers, it was to understand the range of perspectives on how research evidence gets (or doesn’t get) used in planning.
CLINICAL TRIALS: INTERNAL VALIDITY FIRST
Clinical trials present yet another sampling logic. The primary concern is internal validity—being confident that any differences between treatment and control groups are actually due to the intervention, not to some confounding factor.
Here’s where students often get confused: random assignment is not the same as random sampling.
Random assignment is about allocating participants to treatment conditions after they’ve been enrolled. It’s what creates comparable groups and supports causal inference. Random sampling is about who gets into the study in the first place. A trial can have rigorous random assignment while using convenience sampling for enrollment, and most trials do exactly that.
Trial eligibility criteria typically prioritize internal validity over generalizability. You might exclude people with multiple comorbidities, recent medication changes, or complex social situations for clinical or logistical reasons. This creates what’s sometimes called the “efficacy-effectiveness gap”: interventions tested under ideal conditions with carefully selected participants may not work as well in the messy real world.
THE BOTTOM LINE
No sampling method is universally best. Before critiquing a study’s sampling approach, ask yourself: What is this study actually trying to do? A convenience sample that would doom a prevalence study might be perfectly appropriate for a mechanistic laboratory trial. A representative probability would be overkill for an exploratory qualitative study.
15.4 Probability Sampling
Probability sampling encompasses methods where every member of the population has a known, non-zero probability of being selected. This is the gold standard for generalizability because it allows you to quantify sampling uncertainty through standard errors and confidence intervals.
Probability sampling: Selection methods where every population member has a known, non-zero chance of selection. Enables statistical inference to the full population.
But let me be honest: strict probability sampling is often impossible in global health research. It requires sampling frames that don’t exist, resources that aren’t available, and access that can’t be obtained. Still, understanding these methods matters because (a) you’ll need to evaluate studies that use them, and (b) you may be able to approximate them even when perfect implementation isn’t feasible.
SAMPLING ERROR: THE UNCERTAINTY YOU CAN QUANTIFY
Imagine you could measure everyone in your population. That is a census, and it would give you the exact answer, give or take measurement error. But we rarely run a census. It’s usually impossible, and it’s almost always unnecessary. So instead we measure a subset of the population: a sample. Because a sample is only part of the whole, the estimate it gives will sit a little off the true value, and a different subset would land somewhere slightly different. That gap is sampling error: the variability in an estimate that comes purely from measuring some of the population rather than all of it.
The useful thing about sampling error is that it behaves predictably. The larger the sample, the closer to a census, and the smaller the error. But the gains diminish. The scatter shrinks only with the square root of the sample size, so quadrupling the sample halves the spread, and each further gain in precision costs more than the last (Figure 15.3). Under probability sampling, this scatter follows a known distribution, which is what a standard error measures and what a confidence interval reports: not where the truth definitely lies, but how much your estimate would move if you could draw the sample again and again. Known selection probabilities are what make that calculation legitimate.
Sampling error is not the same as bias, and the difference is the most important idea in this section. Sampling error is random, centered on the truth, and shrinks with the sample size. Bias is systematic: a frame that misses the poorest households, a question only literate respondents can answer, the steady losses down the chain of inference (Section 15.2). Bias does not shrink as you collect more data. A larger sample just buys you a more precise estimate of the wrong number. You can quantify sampling error. You can only reason about bias.
This is the real dividing line between probability and non-probability sampling. With known selection probabilities, you can put a defensible number on your sampling error and report an honest confidence interval. Without them, you can still produce a useful estimate, but any standard error you compute rests on assumptions about how people ended up in your sample rather than on the design itself. That’s why the methods below are worth the trouble when you can manage them. It’s also why the rest of the chapter spends so much time on what to do when you can’t.
THE SAMPLING FRAME: WHAT YOU DRAW FROM
Every probability method starts from the same prerequisite. A sampling frame is the operational definition of your population—the list, map, or procedure from which you actually draw your sample. In an ideal world it would match your target population exactly: every member would appear once, and no one else would. We don’t live in that world.
Sampling frame: The list, map, or procedure that defines who can be selected for your study. The quality of your frame determines the quality of your sample.
Frames vary in how close they come to that ideal, and how close you can get fundamentally shapes which studies are feasible. Strong frames, like a health-worker registry, a complete student roster, or a census-mapped household list with GPS coordinates (Seboka et al., 2021), miss almost no one. They are also expensive to build and maintain. Partial frames are more common. CHW household registers, vaccination registries, and clinic patient lists (Choudhury et al., 2022) capture only people who interact with formal systems, and the people they miss tend to be poorer, more rural, and more marginalized. For some populations, no frame exists at all. There is no list of people who inject drugs, sex workers, undocumented migrants, or nomadic Fulani pregnant women (Salifu et al., 2024), so probability sampling isn’t feasible.
A sampling frame doesn’t have to be perfect to be useful. The question is whether its limitations are understood and manageable.
When no frame exists, you can sometimes build one. Door-to-door household listing is the most reliable approach—and the most labor-intensive—which is exactly why DHS field teams spend days enumerating each selected area before any sampling happens (see the multistage cluster method later in this section). You can also construct a frame from administrative records, such as clinic or program registers, or from digital traces like phone numbers. Each carries the same caution: a built frame inherits the gaps of whatever it was built from. Before committing to a sampling approach, assess your frame against these criteria:
| Criterion | Questions to Ask | Red Flags |
|---|---|---|
| Coverage | What proportion of target population is on the frame? | <80% coverage without clear pattern |
| Recency | When was the frame created? How much has population changed? | Frame >2 years old in mobile population |
| Accuracy | Are people on the frame actually in the target population? | High rates of ineligibility when contacted |
| Accessibility | Can you actually access the frame for sampling? | Requires permissions you don’t have |
| Duplicates | Does the frame contain duplicates? | Same person appears multiple times |
If no adequate frame exists and you can’t create one, you’ve learned something important about your design. Probability sampling simply isn’t available, and you’ll turn to the non-probability methods discussed later in this chapter.
SIMPLE RANDOM SAMPLING (SRS)
In simple random sampling, every member of the population has an equal chance of selection, and each selection is independent of the others. Think of drawing names from a hat, or assigning a random number to everyone on a list and taking the smallest ones. This is the baseline every other method is measured against. Because the draws are random and independent, the sampling error follows directly from the sample size, and the standard error behaves exactly as the previous section described.
SRS is also rarely practical in the field. It needs a complete frame of the entire population, and it ignores geography. Two hundred people drawn at random from a rural district could sit in two hundred scattered locations, leaving your field team to spend more time traveling than collecting data. The methods that follow are, for the most part, responses to these two limits: an incomplete frame and dispersed geography.
SYSTEMATIC SAMPLING
SRS has a catch: you need a complete list of the population to draw from, and often there isn’t one. You can’t always compile one before you start, either. What you can usually do is impose an order on the population as it comes to you.
That ordering can take two forms. Sometimes it unfolds in real time: every patient through a clinic door, every house along a road. You select as you go and never compile a full list. Other times you already have an ordered list, and counting off every k-th name is just less work than drawing random numbers, with the bonus that the sample spreads evenly across the frame.
This is called systematic sampling. You pick a random seed number k, and take every k-th member from an ordered population. Divide the population size by your target sample size to get the interval k, choose a random start between 1 and k, then count off. For 500 patients and a target of 50, k is 10, and a random start of 7 selects 7, 17, 27, and so on.
Watch out for periodicity—if your list has a repeating pattern that aligns with your sampling interval, you’ll get biased results. If every 10th household on your list is a corner house (possibly wealthier), sampling every 10th household could systematically over-represent wealthy households.
The one hazard is periodicity. If the ordering hides a repeating pattern that lines up with your interval, you’ll get a biased sample. For instance, if a clinic’s records run in date order and your interval falls on every 7th day, you could end up sampling only Sundays, when a different mix of patients comes in. The remedy depends on which ordering you have. When you hold the list, shuffle it before counting off; randomizing the order destroys any pattern. When you can’t reorder a real-time sequence, choose an interval that won’t line up with a cycle you suspect, and avoid sampling every 7th if arrivals follow a weekly rhythm.
STRATIFIED SAMPLING
A simple random sample leaves who gets in to chance. That’s fine for an overall estimate, but it offers no guarantee about subgroups. A group that’s small in the population, like rural residents or a particular age band, can turn up in numbers too small to say anything precise about. Sometimes that subgroup is exactly what you care about.
Stratified sampling fixes this. You divide the population into subgroups, called strata, then draw a separate sample from each. Every member belongs to exactly one stratum, and you sample within all of them. You might stratify by geography, age, sex, institution, or risk level.
This guarantees every subgroup is represented, and you can size each stratum to get enough of even the small ones. Stratifying can also lower your sampling error: by sampling within strata, you hold the differences between strata constant, so for a given sample size your estimates are at least as precise as SRS, and usually more. Keep that in mind for the contrast with cluster sampling (up next), which moves precision the other way.
Proportionate vs. Disproportionate Stratified Sampling
Once you’ve chosen your strata, you have to decide how many people to draw from each. The right answer depends on what you want the sample to do.
If you want a single estimate for the whole population, sample each stratum in proportion to its size. This is proportionate stratified sampling: if urban areas hold 30% of the population, they make up 30% of the sample.
If you want to compare strata, proportionate allocation can starve the smaller ones. Suppose rural areas hold only 20% of the population but the rural–urban comparison is the point of the study. Proportionate sampling leaves you too few rural respondents for a precise rural estimate. Disproportionate stratified sampling oversamples the smaller stratum—say 50% urban, 50% rural—so both estimates are precise enough to compare. The catch: disproportionate sampling requires survey weights for any population-level estimate. Without them, your results tilt toward the oversampled group.
Choosing Strata
A good stratification variable is one you can actually use and one that matters:
Relevant to your outcomes. Stratify by characteristics associated with what you’re measuring. For a study of healthcare access, urban/rural matters; first letter of surname does not.
Known before sampling. You can only stratify by what you already know for everyone in the frame. Age of household head is often in census lists. Individual mental health status isn’t known until you measure it, so you can’t stratify by it.
Sized in advance. To allocate the sample across strata, you need to know roughly how big each stratum is, usually from census data or prior surveys.
Few enough to be useful. Ten strata and a sample of 200 means about 20 people per stratum—too few for precise subgroup estimates. Keep the number of strata manageable.
CLUSTER SAMPLING
SRS has a second weakness, separate from the frame: geography. Even with a complete list, a random sample of 200 people could scatter across 200 villages, and no field team can afford to reach them all. Often there’s no list of individuals anyway, only a list of places.
Cluster sampling uses groupings that already exist. Most populations come pre-divided into natural units: villages, schools, clinics, city blocks. Rather than sampling individuals, you sample whole units. You randomly select some of those clusters, then study everyone (or a random subsample) inside the ones you picked. The clusters you don’t select drop out entirely.
Stratified and cluster sampling both involve groups, but they use them differently. With strata, you sample within every group. With clusters, you sample which groups, then take the people inside the ones you select.
This is what makes cluster sampling practical for dispersed populations. You draw 10 villages at random, work intensively in each, and build a frame of individuals only for the clusters you actually selected, never for the whole population.
Design effect (DEFF): The ratio of the variance under the actual complex design to the variance under simple random sampling. A DEFF of 2 means you’d need twice as many participants to achieve the same precision as SRS.
The convenience has a cost. People in the same cluster tend to resemble one another. They share an environment, an economy, a clinic, a water source. So each extra person you sample from the same village adds less new information than a person drawn at random from the whole population would. This redundancy inflates sampling error relative to SRS, an effect called the design effect. Stratifying exploits the differences between groups to gain precision; clustering accepts the similarity within groups to gain feasibility.
You manage the design effect by spreading the sample across more clusters. More clusters with fewer people each generally beats fewer clusters with more people each, because a new cluster brings genuinely new information while another household in an already-sampled village brings less.
NoteInnovation: Gridded Population Sampling
Gridded population sampling uses satellite-derived population density estimates to create sampling frames in settings where traditional census data don’t exist or are severely outdated (Thomson et al., 2020). The approach was developed for use in Somalia, a country facing governance challenges and security constraints that preclude traditional census activities, and has since been applied in other fragile settings (Qader et al., 2020).
The process starts with high-resolution (100-meter) population density estimates from sources like WorldPop, which combine satellite imagery, land cover data, and modeling to estimate population distribution. A quadtree algorithm then divides the country into areas with approximately equal population sizes, which reduces variance in sampling weights (Qader et al., 2020). These gridded units are stratified by population characteristics (urban/rural, settled/nomadic) and administrative boundaries, and primary sampling units are selected from them. Field teams then conduct listing and household selection on the ground. To minimize enumerator bias, teams use tablets with built-in randomization: enumerators list all structures in a selected grid cell, and the tablet randomly selects which to visit, eliminating the potential for conscious or unconscious avoidance of certain households.
MULTISTAGE CLUSTER SAMPLING: THE DHS APPROACH
Real national surveys rarely use any of these methods alone. Multistage cluster sampling selects progressively smaller units—regions, then clusters, then households, then individuals—stratifying and clustering at different stages. The Demographic and Health Surveys have refined the approach over decades, and it’s worth following in detail because it shows every method in this section working at once.
Primary Sampling Unit (PSU): The first-stage unit selected in a multistage design. In DHS surveys, this is typically an enumeration area—a geographic cluster of 100-300 households mapped during the census.
Here’s how it typically works, using the Ethiopian DHS as an example:
Stage 1: Select Primary Sampling Units (PSUs)
Using census data, the country is divided into enumeration areas (EAs) or similar geographic clusters. The 2016 Ethiopian DHS used enumeration areas from the 2007 Population and Housing Census as the sampling frame, stratified by region and by urban/rural residence (Seboka et al., 2021). PSUs are selected with probability proportional to size (PPS)—larger EAs are more likely to be selected, which is intuitive: if an EA has twice as many people, it should have twice the chance of being selected to ensure equal representation at the individual level.
Stage 2: Household Listing
Field teams visit each selected EA and conduct complete household listing—going door to door, recording GPS coordinates, and creating a fresh frame of all households in that area. This is arguably the most labor-intensive part of the entire survey. Teams spend days in each EA, mapping structures, identifying residential buildings, and creating numbered household lists. This updated listing is essential because the original census data may be years old, and populations shift.
Stage 3: Household Selection
From the household list, a fixed number of households (often 25-30) are randomly selected using the listing data. In the Ethiopian DHS, researchers selected a fixed number of 28 households per enumeration area through equal probability systematic selection (Seboka et al., 2021). The fixed number per cluster keeps field operations manageable while the PPS selection of clusters ensures population-level representativeness.
Stage 4: Respondent Selection
Within selected households, specific individuals are selected for interview—often all women aged 15-49 and a subsample of men aged 15-59. Children under age 5 in selected households are typically measured for anthropometric indicators.
Step back and notice what the design did. It stratified the country by region and urban/rural (stratification), selected enumeration areas as clusters with probability proportional to size (clustering), and drew households within each cluster by equal-probability systematic selection (systematic sampling), all while keeping a known selection probability at every stage (the SRS ideal). Multistage sampling isn’t a fifth method. It’s the other four arranged in sequence.
Because it clusters, it carries a design effect, which is why DHS surveys run to thousands of respondents. When within-cluster similarity is high—every household in a village drawing from the same water source—each added household in a cluster contributes less new information than a household in a fresh village would. Surveys compensate by sampling more clusters, and sometimes more households per cluster.
NoteTechnical Note: Survey Weights
Multistage designs require survey weights to produce unbiased population estimates. Weights account for:
- Unequal selection probabilities: If some groups were deliberately oversampled (e.g., urban areas) to ensure adequate subsample sizes
- Non-response adjustments: If response rates differed by region or demographic group
- Post-stratification: Adjusting to known population totals from census data
If you analyze DHS data without applying survey weights, your estimates may be biased. Most statistical software has survey analysis procedures specifically for complex samples—in Stata, use the svy prefix; in R, use the survey package.
15.5 Non-Probability Sampling
Most global health studies use non-probability sampling. Convenience samples, purposive samples, and snowball samples dominate the literature, and not only because probability sampling is expensive. Sometimes it isn’t possible: no frame exists and none can be built. Often it isn’t necessary. Most RCTs enroll a convenience sample of eligible volunteers at participating sites, because random assignment, not random sampling, is what protects the treatment comparison.
Non-probability samples can produce valuable knowledge. What matters is understanding what these methods can and cannot support.
CONVENIENCE SAMPLING
Convenience sampling means enrolling whoever is accessible, eligible, and available. The first 100 patients who walk through the clinic door. Students in your research methods class. Respondents to an online survey shared on social media who have school-age children.
Convenience sampling: Selecting participants based on availability and ease of access rather than systematic procedures.
The critique of convenience sampling is well-known: your sample may systematically differ from your target population in ways that bias your results. Patients at a teaching hospital aren’t representative of all patients with that condition. People recruited through social media aren’t representative of people without smartphones or internet access.
But convenience samples aren’t always inappropriate. If you’re piloting a new instrument and care primarily about whether items are comprehensible, a convenience sample is fine. If you’re testing a biological mechanism that should operate similarly across populations, convenience sampling may be acceptable. If you’re studying experiences rather than estimating prevalence, convenience can be defensible.
The key is matching your sampling approach to your research goals, and being honest in your limitations section about what inferences are and aren’t supported.
PURPOSIVE SAMPLING
Purposive sampling involves deliberately selecting participants based on specific characteristics relevant to your research question. Unlike convenience sampling (which is about ease) or probability sampling (which is about representativeness), purposive sampling is about strategic selection for insight.
The variants differ in what they select for. Maximum variation sampling seeks participants who differ on key dimensions. If you’re studying community health worker experiences, you might deliberately recruit CHWs from different regions, different experience levels, and different types of communities. Typical case sampling does the opposite: it selects participants who represent the norm. If most CHWs are women with secondary education serving rural areas, you’d sample exactly that profile. Extreme or deviant case sampling targets the unusual examples, like the spectacularly successful CHW or the one who resigned in frustration, to understand what makes cases exceptional. And key informant sampling selects people whose position gives them insight unavailable from typical participants: district health officers, program managers, traditional leaders.
NoteVenue-Based Sampling
A related strategy for populations with no frame is venue-based sampling (also called time-location sampling). Instead of sampling people, you sample the places and times where the population gathers—bars, clubs, street corners, drop-in centers—and recruit whoever is present. A study of MSM and transgender women in Tijuana, Mexico compared venue-based sampling with RDS in the same population and found that the two methods reached systematically different people (Pines et al., 2021). Venue-based recruitment at bars, clubs, and through social networking apps enrolled more socially integrated participants, who were more likely to be employed and to report hazardous alcohol use. RDS reached more marginalized participants, with higher rates of internalized stigma, deportation concerns, and injection drug use. Both methods produced similar HIV prevalence estimates, but for any characteristic tied to social visibility, the recruitment method shapes who you find.
CHAIN REFERRAL SAMPLING
Some populations appear on no list and no map. People who inject drugs, sex workers, and undocumented migrants are missing from registries by design or by necessity, and a household survey will rarely find enough of them. But members of these populations usually know others like themselves. Chain referral sampling turns those social connections into the recruitment mechanism. Participants refer people they know, who refer people they know. The informal version is snowball sampling. Respondent-driven sampling adds structure to the referral chains so that, in theory, the results can support statistical inference.
Snowball Sampling
Snowball sampling uses existing participants to recruit future participants. You start with a few “seeds,” who refer people they know, who refer people they know, and the sample grows like a rolling snowball.
A study of pregnant women in nomadic Fulani communities in Ghana shows the approach at work. Researchers started with community contacts who could introduce them to pregnant women, and those women identified others (Salifu et al., 2024).
If you’re going to use snowball sampling, do it thoughtfully. Start by choosing diverse seeds, because your sample will reflect your starting points. If all your seeds are urban, educated, and young, your snowball will roll through urban, educated, young networks. Select seeds from different geographic locations, demographic groups, and social positions. Set limits on referral chains, too. Unconstrained snowball sampling can follow one highly connected person’s network indefinitely, so consider capping how many referrals you’ll accept from any one participant or how many “generations” of referral you’ll follow.
As recruitment proceeds, track who refers whom and whether referrals stay within demographic groups or cross boundaries. These patterns tell you what your sample represents and where it may be biased. When participants say they can’t think of anyone to refer, probe gently. Do they know others like themselves but feel uncomfortable referring them? Understanding why referrals don’t happen is as important as understanding why they do. Finally, consider combining snowball sampling with other approaches, such as venue-based recruitment to reach one segment of a population while the snowball reaches another.
A key limitation is that snowball samples over-represent people who are socially connected. Isolated individuals—who may be at highest risk for many health outcomes—tend to be missed.
Think about what this means for specific populations. Among people who inject drugs, snowball sampling reaches those with drug-using peers but may miss those who inject alone. Among sex workers, it reaches those networked with other sex workers but may miss those who work independently. Among undocumented migrants, it reaches those in community networks but may miss the most transient or isolated individuals.
Snowball sampling tells you about people in networks. By design, it cannot tell you about people outside networks.
Respondent-Driven Sampling (RDS)
Respondent-driven sampling attempts to combine snowball sampling with statistical corrections to approximate probability sampling. It’s widely used for HIV surveillance among key populations like people who inject drugs, sex workers, and members of sexual minority groups.
Respondent-driven sampling (RDS): A chain-referral sampling method that uses statistical weights to adjust for network structure, theoretically allowing inference to the broader hidden population.
The mechanics are more structured than simple snowball sampling. Researchers start by recruiting a small number of initial participants, or “seeds,” who are diverse on key characteristics. Each seed receives a fixed number of coupons, typically 2-3, to recruit peers from their network. Recruits who meet eligibility criteria and haven’t previously enrolled can participate, and they receive their own coupons to recruit additional peers. Participants typically receive one incentive for their own participation and a smaller incentive for each peer who successfully enrolls using their coupon. Because coupon numbers link recruiters to recruits, researchers can analyze recruitment patterns and network structure.
The theoretical foundation of RDS is that, given certain assumptions about network structure and recruitment dynamics, the resulting sample’s composition will eventually become independent of the initial seeds and reflect the broader population’s characteristics. Statistical weights can then adjust for the fact that well-connected individuals are more likely to be recruited than isolated individuals.
Studies in Ukraine used RDS to estimate HIV and HCV prevalence among people who inject drugs across five cities (Zelenev et al., 2019). The approach allowed researchers to reach individuals who would never be captured in any registry-based frame.
But the Ukrainian studies also revealed RDS limitations. The research team found that RDS samples showed geographic concentration—in Kyiv, more than 80% of RDS-recruited participants came from only 3 of the city’s 10 neighborhood districts, whereas random sampling of people in opioid agonist therapy programs captured participants from all 10 districts. Social networks tend to be geographically clustered, and RDS inherently samples within networks rather than achieving geographic dispersion.
WarningRDS Isn’t Magic
RDS proponents sometimes present it as a way to generate representative samples from hidden populations. Critics argue that the statistical assumptions—including assumptions about random recruitment within networks, accurately reported network sizes, and equilibrium being reached—are rarely met in practice.
At minimum, RDS estimates should be interpreted with more caution than traditional probability samples. Don’t treat RDS standard errors as if they have the same meaning as standard errors from a stratified random sample.
MIXING SAMPLING METHODS
Real-world research often combines sampling approaches. The study of nomadic Fulani women in Ghana combined systematic enumeration with snowball referrals (Salifu et al., 2024). The Ukrainian HIV surveillance combined RDS with venue-based sampling in some analyses (Zelenev et al., 2019).
Mixed sampling approaches can strengthen studies. In sequential designs, purposive sampling identifies key informants who can inform probability sampling frame development. In parallel designs, you recruit some participants through probability methods and others through network methods, then compare. In embedded designs, you conduct purposive qualitative sampling within a probability-sampled survey. The key is being explicit about what each sampling component contributes and what inferences each supports.
SPECIAL CONSIDERATIONS FOR MULTI-SITE STUDIES
Many global health studies operate across multiple sites—different clinics, districts, countries. The most common version is the multi-site clinical trial, which recruits at several hospitals or clinics to reach its enrollment target faster and to test the intervention in more than one setting.
In a multi-site trial, site selection is itself a sampling decision, and rarely a representative one. Sites are chosen for enrollment capacity, research infrastructure, existing partnerships, and willing investigators. Within each site, enrollment is typically a convenience sample of eligible patients who present during the trial. None of this threatens internal validity: randomization happens after enrollment and is usually stratified by site, so the treatment comparison stays fair within each one. What it affects is generalizability and transportability. The move from “all possible sites” to “selected sites” is an extra link in the inference chain, so when you read a multi-site trial, ask whether the effect was consistent across sites and whether those sites resemble the settings where the intervention would actually be used.
Multi-site observational studies face a further tension between standardization and local adaptation. A diabetes care study across 42 LMICs illustrates it (Flood et al., 2022): standardized sampling procedures would enable cleaner cross-country comparisons, but contexts differed so much that rigid standardization would mean excellent procedures in some settings and inappropriate ones in others. The usual compromise is standardized principles with locally adapted implementation. Set minimum standards every site must meet, such as random selection at the final stage, document exactly what each site did, and account for site in the analysis. When you pool data, weight sites by the population they represent if you want estimates for a broader region; weight them equally if you only want to characterize your partner sites.
Multi-site studies trade depth for breadth. What you gain in external validity by including diverse contexts, you may lose in the precision of your sampling within any single context.
15.6 Recruitment
A sampling plan specifies who should be in your study. Recruitment is the work of actually enrolling them: finding eligible people, explaining the study, and getting them to say yes. The best sampling design means nothing if you can’t do this part. And unlike sampling, recruitment can’t be worked out entirely on paper. It depends on understanding communities, building trust, navigating gatekeepers, and communicating clearly about what participation involves.
COMMUNITY-BASED RECRUITMENT
In many global health contexts, successful recruitment begins with community engagement long before any enrollment happens. Community health workers are often the entry point. They have existing relationships with households and can introduce research in a trusted context. In rural Nepal, CHWs conducted household enumeration as part of routine service delivery, which simultaneously created a sampling frame and built community familiarity with the research team (Choudhury et al., 2022). Local leaders and gatekeepers matter just as much. Village chiefs, religious leaders, women’s group coordinators, and other community figures can facilitate or block access, and their endorsement signals legitimacy. For longer-term or more sensitive research, a formal community advisory board provides ongoing input on recruitment strategies, compensation, and communication. And sometimes there’s no substitute for physically visiting households. Door-to-door enumeration is resource-intensive, but it creates direct contact with potential participants.
CLINIC-BASED RECRUITMENT
Many studies recruit from health facilities—hospitals, clinics, antenatal care sites. This is efficient, but it has its own challenges. Clinical gatekeepers control access: the nurse who manages patient flow, the receptionist who sees everyone first, the doctor who decides whether to mention the study. Patient flow creates timing constraints, because a busy ANC clinic may have only narrow windows when patients are waiting and available for a recruitment conversation. And research must not disrupt care. If recruitment slows clinical operations or patients feel pressured, you’ll lose access quickly. Above all, remember that clinic samples miss people outside the system. The most marginalized community members—those without documentation, without money for transport, without trust in formal healthcare—won’t appear at facilities.
DIGITAL RECRUITMENT
Digital recruitment reaches potential participants through phones and the internet rather than in person. It includes mobile phone surveys conducted by live interviewers, SMS, or interactive voice response, with respondents often selected by random digit dialing; advertisements on social media platforms; outreach through messaging apps like WhatsApp; and online panels of pre-recruited respondents. The advantages are speed, scale, geographic reach, and relatively low cost per respondent. But the evidence on how digital methods compare to traditional approaches is sobering.
A multi-country study directly compared mobile phone surveys (MPS) to nationally representative face-to-face household surveys in six LMICs: Ecuador, Malawi, Morocco, Mumbai (India), Sri Lanka, and Zambia (JA et al., 2025). The researchers employed random digit dialing for MPS and compared results to WHO STEPS surveys conducted in the same countries.
The findings were nuanced. In settings with high mobile phone ownership, MPS estimates approximated household survey estimates reasonably well for some indicators. But MPS systematically under-represented older individuals, rural populations, people with lower education levels, and disabled persons. The degree of bias correlated with mobile phone penetration: in countries where phone ownership was unevenly distributed across demographic groups, MPS estimates diverged more from face-to-face survey estimates (JA et al., 2025).
A separate systematic review of remote data collection modes found that response rates and data quality varied substantially across LMICs—more so than would be expected from high-income country experience (Greenleaf et al., 2017). What works in one context may fail in another.
Digital exclusion is systematic, not random. Whoever your digital recruitment misses, it’s probably not missing at random across demographic groups.
Digital recruitment works best when your target population has high digital access, when you’re studying populations defined by online behavior or communities, when speed and cost are critical constraints, when geographic reach is important and travel is prohibitive, or when you’re willing to acknowledge and potentially adjust for coverage bias. It’s riskiest when your target population is elderly, rural, or has limited education; when you need estimates generalizable to a full population; when digital access varies dramatically within your target group; or when you’re measuring outcomes that correlate with digital access itself.
NETWORK-BASED RECRUITMENT
If your design uses chain referral (snowball sampling or RDS), recruitment runs through participants rather than research staff. Enrollment depends on people you don’t employ: participants have to pass along coupons, vouch for the study, and reassure peers that joining is safe. The practical work follows from that. Prepare participants for the recruiter role by briefing them on what to say about the study, who is eligible, and what not to promise. Make referral easy and discreet, with coupons that don’t disclose why the bearer was referred and study sites that members of the population can visit without being noticed. Compensate the act of referral as well as participation. And monitor the referral chains as they grow, so you notice quickly when recruitment stalls or collapses into a single subgroup. Organizations that already serve the population, like harm reduction programs or sex worker collectives, can provide credible first seeds and trusted venues.
ETHICAL CONSIDERATIONS IN RECRUITMENT
This isn’t the ethics chapter, but some recruitment principles are essential.
Participation must be voluntary, and recruitment can compromise that in subtle ways. If the nurse at your clinic is telling patients about the study, can those patients really feel free to decline? Power dynamics matter, especially when gatekeepers introduce studies, when compensation is substantial relative to local incomes, or when participants depend on the recruiting institution for other services. Compensation requires the same balance: it should recognize participants’ time and expenses without being so high that it compromises voluntary choice. There’s no universal formula. What’s appropriate depends on local wages, travel costs, time requirements, and cultural expectations, and what counts as appropriate in Nairobi differs from rural Bihar.
Recruitment messages, for their part, should be honest about what participation involves, what risks exist, and what participants will and won’t receive. No overselling the benefits. No minimizing the burdens. Describing your recruitment plan and including sample materials is part of the ethical review process.
COMMON RECRUITMENT CHALLENGES
Common recruitment challenges include gatekeepers who won’t grant access, eligible people who refuse, samples that drift away from their targets, and populations that stay hidden behind stigma or legal risk.
A gatekeeper who won’t help usually has a reason—protectiveness toward the community, wariness of extractive research, or simple overwork—and the response depends on which one you’re facing: another entry point, something of value offered in return, or patience while trust builds. Refusals call for listening rather than persistence: ask decliners why they said no, and review the recruitment script for length and jargon, since sometimes the fix is as simple as a different messenger or a different time of day.
Sample drift is harder to catch than the first two challenges: three months in, a stratified design has filled with easy-to-reach participants, and you’ll only notice if you review the sample’s demographic composition as you go. A weekly review lets you shift effort toward the lagging strata while there’s still time to close the gap.
Hidden populations are the hardest case because no recruitment script will surface people whom stigma or legal risk keeps out of view. The way in is through trusted community partners and network- or venue-based recruitment, paired with transparency about the coverage you can’t achieve.
If recruitment is going badly, don’t just push harder with the same approach. Stop and diagnose the problem:
- Are you reaching eligible people? (If not: access/frame problem)
- Are eligible people refusing? (If yes: recruitment approach problem)
- Are enrolled people dropping out? (If yes: retention problem)
And remember, the best solution to most recruitment challenges is prevention through early, proactive planning.
RETENTION
For longitudinal studies, recruitment doesn’t end at enrollment, because participants must return for follow-up visits, answer the next survey wave, and remain findable. Keeping every participant is unrealistic; the goal is to keep attrition low and non-systematic. The latter can be hard because people drop out for reasons that correlate with the outcomes you’re studying—migration, illness, job loss—so when the most vulnerable participants are the most likely to disappear, the surviving sample drifts further from your target population with every wave. This differential attrition biases results in ways a larger starting sample can’t fix.
I mention retention in this section on recruitment because retention success begins at the recruitment stage. Whether you can find a participant a year from now depends on whether you collected multiple contact methods at baseline. Whether they want to come back depends on whether recruitment set honest expectations and made the first contact a good experience. Whether the community helps you re-engage people who move depends on the partnerships you built before enrollment began. The rest is consistency: flexible scheduling, modest incentives, and contacts kept as low-burden as possible.
A study tracking newborn health outcomes in Bangladesh shows retention engineered into the design from the start (Jahan et al., 2022). The team embedded the research within care pathways: transportation assistance helped families reach referral facilities, coordination with receiving hospitals ensured that participants who needed additional care received it, and a physician’s independent repetition of 20% of CHW assessments maintained regular contact while assuring data quality. Participation carried tangible benefits at low burden, and retention followed.
15.7 Reporting Sampling Methods
A reader of your methods section is asking one question: does the sampling support the inferences you draw? Your job as an author is to answer that question before the reader has to ask it. Start with the target population: define it explicitly and keep your conclusions matched to it, because sampling clinic patients and writing about the community is scope creep. “Depression prevalence among clinic patients” is not the same claim as “depression prevalence in the community.”
Everything in this section applies to critical appraisal as well. When you read someone else’s methods section (Chapter 5), check for the same elements—and treat a convenience sample paired with broad generalizations, or missing response rates, as red flags.
From there, the elements to report track the chain of inference, and a reader should be able to reconstruct the path from your target population to your actual sample. Describe the constraints that limited who you could reach, and identify the sampling frame—the list, map, or procedure you sampled from—along with its source and known limitations. Name your sampling method explicitly (simple random, stratified, cluster, convenience, purposive, snowball, RDS), then describe the mechanics: how people were selected, by whom, and when. Report both intended and actual sample sizes, explain any gap between them, and give response rates (for longitudinal studies, retention rates at each follow-up). Finally, describe the demographic characteristics of your actual sample and acknowledge what populations or perspectives your sampling may have missed.
It’s important to show that the sampling fits your purpose. A prevalence study should use probability sampling or explain how it addresses representativeness without it. A causal study can defend a narrower sample if the comparison groups are sound. A qualitative study should describe its purposive strategy and show that it captures relevant variation. And state plainly what your sampling cannot support, rather than claiming broad generalizability from a narrow sample and leaving the reader to spot the leap.
Here’s a model paragraph for a hypothetical study, drawing on elements from several studies we’ve discussed:
We used multistage cluster sampling to select a representative sample of households in the district. First, we randomly selected 30 enumeration areas (EAs) from the 2019 census frame with probability proportional to population size, stratified by urban and rural residence. Within each selected EA, field teams conducted complete household listing, identifying 2,340 households across all EAs. From each EA’s household list, we systematically sampled 25 households, yielding an intended sample of 750 households. Of these, 712 households (95%) completed interviews; 38 were unreachable after three visits (n=22), refused (n=14), or had no eligible respondent (n=2). All analyses apply survey weights to account for stratification and clustering.
In a few sentences, this paragraph names the method, the frame, the stratification, the selection procedure at each stage, the intended and actual sample sizes, the response rate and the reasons for non-response, and the analytical plan for weights, everything a reader needs to evaluate the sampling and interpret the findings.
The common reporting mistakes are the mirror image of that example. Vague selection is the most frequent: “participants were recruited from clinics” doesn’t tell the reader whether that meant everyone who showed up during a period, a random sample from patient lists, or anyone who responded to flyers. Missing response rates leave readers unable to assess selection bias, and omitted exclusion criteria hide what the eligibility rules did to generalizability. Don’t claim probability sampling when it wasn’t: approaching “consecutive patients” is systematic convenience sampling, not probability sampling. And if you used cluster sampling, acknowledge the design effect and analyze accordingly.
15.8 Closing Reflection
It’s worth stepping back from the technical details to consider what sampling decisions mean. When you design a sampling strategy, you’re deciding whose lives will shape the evidence. Every choice—where to recruit, what criteria to apply, how much effort to spend reaching hard-to-access populations—determines whose experiences count. These are ethical decisions as much as methodological ones.
As you design your own studies, ask: Whose voices might this sampling approach miss? Are the populations most affected by this health problem represented? What do my sampling choices reveal about my assumptions?
Consider what happens across an entire field of research. If studies of maternal depression consistently sample from urban clinics, studies of childhood nutrition from accessible villages near research institutions, and studies of HIV treatment from patients already engaged in care, then the evidence base systematically reflects the experiences of more accessible, more connected, more visible populations. The hardest-to-reach communities—nomadic populations like the Fulani women in Ghana (Salifu et al., 2024), people who inject drugs in hidden networks (Zelenev et al., 2019), residents of conflict-affected areas where no census exists (Qader et al., 2020)—are studied rarely, and often with methods that don’t support strong inference. Evidence generated from some populations gets applied to others. When sampling consistently over-represents certain communities and under-represents others, the evidence base itself becomes inequitable.
There’s a structural tension here: the populations most important to reach are often the hardest to sample rigorously. You can achieve a beautiful probability sample of patients attending a well-organized urban clinic. But the patients who can’t afford transport, who distrust the medical system, who have disabilities that prevent clinic attendance aren’t in that sample, no matter how rigorous the methodology. RDS can estimate HIV prevalence among people who inject drugs who are connected to social networks, but the most isolated, most at-risk individuals have, by definition, smaller networks and lower chances of being recruited through chain referral. Innovations like gridded population sampling extend probability methods into contexts where traditional approaches fail (Thomson et al., 2020), but they remain expensive and technically demanding. Innovation requires resources, and resources flow toward some populations more readily than others.
So what can you do? The reporting practices from the last section are the starting point: state who your sample represents and who it doesn’t, and acknowledge who was left out. Beyond that, track refusal rates by demographic characteristics when you can, and name what it would take to reach the populations your study misses. Even when you can’t reach them this time, naming the gap tells the field what remains unknown. And before you default to a convenient sample, ask whether investment in access would be possible.
I don’t want to overstate this. Most studies face legitimate constraints of budget, time, logistics, and safety, and convenience sampling isn’t inherently unethical. The ethical question is whether you’re making deliberate choices with awareness of their implications or simply defaulting to what’s easy. The communities most affected by global health challenges deserve to have their experiences inform the evidence meant to help them.
One question this chapter has deliberately left open: how many participants do you need? Sampling determines who gets into your study and how. How many you need is a different calculation, and it’s the subject of the next chapter on power and sample size.
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