5  Methods Comparison

The preceding chapters presented detailed findings for each of the five alternative methods evaluated in this study — Network Scale-Up Method (NSUM), Adaptive Sampling (AS), Lot Quality Assurance Sampling (LQAS), Administrative Records Review (ARR), and Rapid Convenience Monitoring (RCM) — alongside the gold-standard multistage cluster coverage survey. This chapter compares the methods against the gold standard and each other, and draws conclusions about their suitability for routine zero-dose measurement in settings like Kano. The gold standard yielded Penta-1 coverage estimates of 66.8% in Gabasawa, 62.1% in Gaya, 74.7% in Nassarawa, and 61.7% in the combined non-sentinel stratum; these figures are the benchmark throughout.

5.0.1 Evaluation Framework

Comparing methods that were not designed for identical purposes requires an explicit evaluative lens. We assess each method against six criteria that capture the practical and statistical trade-space programs must navigate when choosing a measurement approach.

Statistical criteria cover three dimensions: bias (are estimates systematically above or below the gold standard?), precision (how tightly bounded are the estimates?), and efficiency (how much precision does the method deliver per unit of cost relative to a direct probability sample?). Logistical criteria cover three more: scale and time (the minimum geographic scope the method requires, and the calendar time from commissioning to results), analytic complexity (the statistical expertise required to design, implement, and correctly analyze the method), and operational burden (field logistics, training, and cost, both per-interview and total). A method may perform well on one dimension while failing on another; the appropriate choice always depends on the programme decision at hand.

5.0.2 Overview of Results

5.0.2.1 Method Profiles

Table 5.1 summarizes each method’s estimand, inferential basis, and primary programmatic use.

Table 5.1: Method summary

Method	Estimand	Inferential basis	Primary use
GS	Vaccine coverage / zero-dose prevalence + count estimate	Design-based probability sampling	Vaccine coverage and/or ZD prevalence estimation; more generally multipurpose (many questions/indicators)
NSUM	Percentage and number of households with an unvaccinated child	Design-based probability sampling + network scale-up	ZD prevalence and count estimation
AS	Vaccine coverage / zero-dose prevalence + count estimate	Advanced design-based probability sampling	Conditional efficiency gains for clustered zero-dose totals
LQAS	Ward coverage classification; LGA-level prevalence (ZD or coverage)	Small-sample hypothesis test per lot; secondary pooled estimate	Supervisory pass/fail classification
ARR	Vaccine coverage / zero-dose prevalence + count estimate	Relies on correctness of physical registers and accurate geospatial population	Desk-based prevalence estimation (i.e., low- or no primary data collection); Trend tracking
RCM	Number/proportion of ZD children found	Non-probability (not generalisable beyond the walked corridor)	Operational gap identification and mop-up referral

5.0.2.2 Performance Against the Gold Standard

Table 5.2 summarizes how each method performed across the evaluation criteria.

Table 5.2: Comparative performance across the evaluation criteria

Method	Bias vs gold standard	Precision	Efficiency	Scale / time	Analytic complexity	Operational burden
NSUM	High - VF-adjusted variant overcorrects; estimates diverge and not as a stable offset	Medium - low; Precision decreases quickly due to respondent's reporting of network	Medium - When it is unbiased, a network size of 10.8 is more efficient than the GS but less efficient than other NSUM applications with larger networks	Medium - NSUM's selling point is a lower sample size requirement	Medium - Point estimation is simple but variance estimation requires survey software	Medium - households must be sampled probabilistically, but typically with lower sample sizes
AS	Small - field estimates broadly tracked the gold-standard benchmark; sentinel simulation was approximately unbiased	Medium - Field AS lowered standard error versus preliminary estimates in most LGAs; original sentinel simulation often tied matched-budget PPS, while Empirical Bayes Adaptive Sampling improved precision in most sentinel comparisons	Medium - Potential gains depend strongly on adaptive rule; Empirical Bayes Adaptive Sampling was more efficient in simulation but adds complexity	Medium - Can be designed at coverage-survey budgets, but requires a preliminary and adaptive phase	High - Expert statistical analyst required	Moderate to high; real-time analytic capacity and adaptive field routing are binding constraints
LQAS	Medium - Unbiased in theory, but found modest differences with GS unexplained by chance alone	Low - LQAS problems are typically not powered to find small effects with high confidence	High for classification relative to cost; low for prevalence estimation	Medium - Sample size of 19 is considered small, but 1-child per EA slows data collection	Moderate - When weighted classification is used, survey software is typically needed	Low - LQAS generally quick and simple to implement
ARR	High - systematic differences from gold standard made estimates unusable	Not applicable — no sampling uncertainty quantified; values sometimes exceed 100%	Not applicable — no children sampled.	Low - Desk-based estimation (or with lite audit data collection) makes the method fast	Low - Basic GIS skills may be needed to calculate denominator	Low - The low/no-data collection aspect reduces burden substantially
RCM	High - Likely high bias unless catchment area is very small and well-canvassed by enumerator's walk	Low - Even in the best case scenario where sampling bias is zero, a sample of 20 children has very high sampling error	Low - Serial autocorrelation of walking path suggests efficiency lower than a simple random sample	Low - Data collection is very fast (3-4 days per RCM, less if multiple enumerators are deployed simultaneously)	Low - Very simple tabulation templates	Low - Very low logistical footprint

The table above collapses several dimensions into text cells. Figure 5.1 lets you explore any two evaluation dimensions simultaneously as a scatter plot. Each method was scored by the research team on a 1–5 scale for each dimension, and is only meant as a visual representation of the table above.

#| '!! shinylive warning !!': |
#|   shinylive does not work in self-contained HTML documents.
#|   Please set `embed-resources: false` in your metadata.
#| viewerHeight: 600
#| standalone: true

library(shiny)
library(dplyr)
library(ggplot2)

has_ggrepel <- requireNamespace("ggrepel", quietly = TRUE)

scores <- tibble::tribble(
  ~Method,          ~bias, ~prec, ~eff, ~speed, ~analysis, ~ops,
  "Gold standard",     5,     5,    3,      1,        3,     1,
  "NSUM",              2,     2,    2,      2,        1,     3,
  "AS",                5,     3,    3,      1,        1,     2,
  "LQAS",              4,     3,    4,      4,        3,     4,
  "ARR",               1,     1,    1,      5,        4,     5,
  "RCM",               2,     1,    1,      5,        5,     5
)

# Dropdown labels: short, no scale text
ui_labels <- c(
  bias     = "Bias",
  prec     = "Precision",
  eff      = "Efficiency",
  speed    = "Speed",
  analysis = "Analysis",
  ops      = "Operations"
)

# Axis titles: you can keep the full descriptors and scales here
axis_labels <- c(
  bias     = "Low bias (1 = severe, 5 = none)",
  prec     = "Precision (1 = unquantified/none, 5 = high)",
  eff      = "Efficiency (1 = low, 5 = high)",
  speed    = "Speed / small scope (1 = large/slow, 5 = fast/small)",
  analysis = "Analytic simplicity (1 = specialist needed, 5 = straightforward)",
  ops      = "Low operational burden (1 = high burden, 5 = low burden)"
)

method_colors <- c(
  "Gold standard" = "#2c7bb6",
  "NSUM"          = "#d7191c",
  "AS"            = "#1a9641",
  "LQAS"          = "#fdae61",
  "ARR"           = "#756bb1",
  "RCM"           = "#636363"
)

# Fixed-seed jitter so points do not jump when you change dimensions
set.seed(42)
scores_j <- scores |>
  mutate(
    Method = as.character(Method),
    jx = runif(n(), -0.13, 0.13),
    jy = runif(n(), -0.13, 0.13)
  )

ui <- fluidPage(
  fluidRow(
    column(
      6,
      selectInput(
        "xdim", "X-axis:",
        choices  = setNames(names(ui_labels), ui_labels),
        selected = "ops"
      )
    ),
    column(
      6,
      selectInput(
        "ydim", "Y-axis:",
        choices  = setNames(names(ui_labels), ui_labels),
        selected = "bias"
      )
    )
  ),
  uiOutput("warn"),
  plotOutput("scatter", height = "370px")
)

server <- function(input, output, session) {

  output$warn <- renderUI({
    if (input$xdim == input$ydim) {
      tags$p(
        style = "color:#c0392b; font-style:italic; margin:4px 0;",
        "Please select two different dimensions."
      )
    } else if (!has_ggrepel) {
      tags$p(
        style = "color:#7f8c8d; font-style:italic; margin:4px 0;",
        "Note: ggrepel is not available in this environment; using simple text labels."
      )
    }
  })

  output$scatter <- renderPlot({
    req(input$xdim != input$ydim)

    dat <- scores_j |>
      mutate(
        x  = .data[[input$xdim]],
        y  = .data[[input$ydim]],
        xj = x + jx,
        yj = y + jy
      )

    base <- ggplot(dat, aes(x = xj, y = yj)) +
      geom_point(aes(color = Method), size = 3.6, alpha = 0.88) +
      scale_color_manual(values = method_colors) +
      scale_x_continuous(
        limits = c(0.5, 5.9),
        breaks = 1:5,
        labels = as.character(1:5)
      ) +
      scale_y_continuous(
        limits = c(0.5, 5.9),
        breaks = 1:5,
        labels = as.character(1:5)
      ) +
      labs(
        x = axis_labels[[input$xdim]],
        y = axis_labels[[input$ydim]]
      ) +
      theme_minimal(base_family = "sans") +
      theme(
        legend.position = "none",
        panel.grid.minor = element_blank(),
        plot.background = element_rect(fill = "#fafafa", color = NA),
        panel.background = element_rect(fill = "#fafafa", color = NA),
        axis.title = element_text(size = 11),
        axis.text = element_text(size = 10)
      )

    if (has_ggrepel) {
      base +
        ggrepel::geom_text_repel(
          aes(label = Method, color = Method),
          size = 3.2,
          min.segment.length = 0,
          box.padding = 0.25,
          point.padding = 0.15,
          seed = 42,
          max.overlaps = Inf
        )
    } else {
      base +
        geom_text(
          aes(label = Method, color = Method),
          vjust = -0.8,
          size = 3.2,
          show.legend = FALSE
        )
    }
  })
}

shinyApp(ui, server)

Figure 5.1: Methods comparison app (choose X and Y dimensions).

5.0.3 The Missing Middle

A striking structural finding emerges when the five methods are viewed together: they cluster at the extremes of the scale–accuracy spectrum. At one end sits our gold-standard multistage cluster survey — a large, rigorously designed probability sample powered to detect small changes for sentinel-Local Government Area (LGA) coverage evaluation. At the other end are the rapid, small-sample methods: RCM visits 20 children per ward, and LQAS in its classification mode draws only 19. LQAS is often perceived as occupying a middle tier between full-scale probability surveys and rapid methods, and when lots are treated as strata and aggregated to produce a coverage estimate — as in the present study — that perception has some merit. However, the primary objective of LQAS is lot-level classification, not coverage estimation; not all implementations are even designed to support aggregation, and when they are it remains a secondary objective. The operational parameters that follow from that classification objective — small per-lot samples and relaxed error tolerances — place it squarely at the small-sample end of the spectrum with regard to classification.

The two methods that seemed most promising for closing this gap — NSUM and ARR — were unfortunately the two that fared worst on statistical validity. NSUM was expected to borrow information from respondents’ social networks, reducing the required sample size; ARR appealed because the data already exist and require no fieldwork. Both promises proved difficult to keep. NSUM was hampered by a restricted effective network (roughly 11 eligible alters per respondent) and pervasive transmission errors — respondents frequently could not report the vaccination status of contacts’ children. ARR was hampered by inflated District Health Information System (DHIS2) numerators and imprecise population denominators, leaving even the best-performing variant ≈24 percentage points above the gold standard. Some of these data-quality limitations were well documented before the study began and could have been anticipated ex ante. Open questions remained, however, as to whether the innovations the study introduced — in particular, geospatial population estimates for the denominator and Primary Health Center (PHC)-register audits to calibrate inflated DHIS2 numerators — would be sufficient to close the gap. The findings give a clear answer: those innovations were not enough.

The conclusion is not that a true middle ground is impossible; rather, it points to a tendency to underestimate how much can be achieved by re-parameterizing probability sampling itself. A cluster coverage survey with a smaller sample or narrower geographic scope is still a probability survey — it simply yields wider intervals or covers fewer domains. LQAS, itself a probability method, illustrates the point: by fixing inference to a classification question, it achieves actionable outputs with n = 19 per ward. The distinction between the gold standard and rapid alternatives is better understood as a continuum of probability designs, not a gap between paradigms. The classical World Health Organization (WHO) 30-cluster, 7-child Expanded Programme on Immunization (EPI) coverage survey is one illustration of a design that sits between these extremes: a medium-sized probability survey targeting a single-round coverage estimate with roughly ±10-percentage-point precision under standard design assumptions — smaller than the powered-for-change gold standard implemented here, but substantially larger per domain than LQAS or RCM. Detecting change between rounds, rather than estimating a single round, is a distinct requirement that depends on the combined variance of both rounds and generally calls for larger per-round samples than the 30×7 design provides.

5.0.4 Method-by-Method Assessment

5.0.4.1 Gold Standard

The gold standard — a Probability Proportional-to-Size (PPS) multistage cluster design — remains the only method with full design-based validity across all domains and estimands evaluated. Its principal limitation is scale and cost: the Kano baseline required over $870,000 and three months of field work, driven by the study’s dual objective of establishing a baseline and powering future impact evaluation in sentinel LGAs. Smaller or more targeted probability surveys can achieve the same inferential legitimacy at lower cost.

5.0.4.2 Adaptive Sampling

AS produced two distinct kinds of evidence. The non-sentinel field implementation showed that the adaptive step could use information collected during fieldwork. For zero-dose totals, the adaptive sampling estimator had a lower estimated standard error than the preliminary estimator in 10 of 12 non-sentinel LGAs. Across all 12 LGAs, the average estimated standard-error reduction was about 6%; among the 10 LGAs where the adaptive sampling estimator had lower estimated standard error, the average reduction was about 14%. That is a within-design comparison, not a comparison with a conventional survey of the same total size.

The simplified sentinel resampling simulation asks the planning question more directly. In Nassarawa, where zero-dose children were more spatially clustered, the adaptive sampling estimator beat a matched-budget conventional PPS sample in several low-budget, mid-\(\phi\) designs. Outside that coherent Nassarawa pattern, most sentinel simulation cells were near ties or conventional-better. A few Gabasawa and Gaya cells also favored AS, but the wins were narrower and less stable.

A retrospective variant of the design — Empirical Bayes Adaptive Sampling — was much more competitive in the same sentinel exercise. It updates the PPS size measure using preliminary zero-dose risk, rather than routing purely on local neighbors, so the adaptive draw retains a population-scaled baseline. This variant was not fielded and was tested only retrospectively, so it should be read as a promising direction for prospective validation rather than as a settled recommendation. It does, however, indicate that the modest gains of the fielded rule reflect that specific design rather than a general limit of adaptive sampling.

The practical appeal of the fielded AS design therefore depends on conditions that are hard to verify before the survey. The adaptive supplement helps only when the preliminary sample detects enough spatial signal to route effort toward high-yield neighboring Primary Sampling Units (PSUs). That signal depends on the spatial correlation structure of zero-dose status at the PSU scale, which is rarely known well in advance. The design also carries a substantial complexity penalty: real-time estimation, adaptive field routing, Rao-Blackwell reordering, and careful variance diagnostics all require specialist statistical capacity. This complexity is not visible in the apportioned cost breakdown in Table 4.11, which shows lower analysis-phase spend for AS than for the gold standard: shared analytic infrastructure for the core survey (sample frame construction, weighting, and design-based variance estimation) was apportioned across the gold standard, NSUM, and AS in proportion to successful interview counts (Chapter 4), so the gold standard absorbed the larger share of work that AS also depended on. A standalone AS implementation would have to carry that infrastructure on its own.

Some of this analytic complexity is tractable through better tooling, but not all of it. Variant choice matters: classical adaptive cluster sampling, for example, does not control final sample size in the same way as the adaptive web sampling rule used here, and other adaptive families carry their own implementation pitfalls. Off-the-shelf software for adaptive designs is also limited, so teams have often built bespoke analytic pipelines, and tooling is improving only gradually. Planning and analysis therefore still benefit from skilled survey-statistician input.

In the implementation tested here, AS is best viewed as a conditional option for clustered zero-dose totals, not as a routine replacement for same-size conventional PPS sampling.

5.0.4.3 LQAS

LQAS performed as designed, classifying 32 wards in the three sentinel LGAs as acceptable or potentially unacceptable relative to a 50% Penta-1 coverage threshold (n = 19 per ward; decision threshold d* = 13; both error rates < 10%). Eight wards were flagged as potentially unacceptable (two in Gabasawa, five in Gaya, one in Nassarawa). Pooled aggregate estimates were reasonably close to the gold standard for most strata, although one stratum (Nassarawa) was considerably off.

Use of weighted classification bounds (rather than simple decision rules) is likely needed to allow estimates to be credible given the complex sampling design. Both address longstanding implementation fidelity concerns without materially increasing cost.

5.0.4.4 ARR

Every ARR variant materially over- or under-estimated Penta-1 coverage relative to the gold standard. Even the strongest configuration, using PHC-audit calibrated numerators with geospatial denominators, had a mean absolute difference of 24 percentage points and showed no meaningful agreement. As a result, ARR estimates are not suitable as standalone measures of coverage. This finding is consistent with a broader body of work that has reached similar conclusions across other settings.

5.0.4.5 RCM

In this head-to-head exercise, most of the sentinel-area RCM estimates could be made to track the gold standard, but only when we defined the comparison area to hug the walked corridor (a buffered path around the route). That is an appropriate way to evaluate what RCM actually observed, and it also exposes the central limitation: a single walk produces a route-defined snapshot whose meaning does not automatically extend to the wider catchment area decision-makers may care about. Vaccination status also clusters along the walk (serial autocorrelation; OR ≈ 2.35), which further shrinks the effective information in a 20-child sample and makes any best case precision assumptions optimistic.

These results do not support RCM as a generally useful method for program decisions. The likely real-world use case is precisely where its weaknesses bite hardest: catchment areas larger than the corridor covered before hitting a 20-child quota, where bias can be substantial and uncertainty remains large even under generous assumptions. In relation to the objective of finding zero-dose pockets, the hotspot comparisons reinforce the same message: in several wards, the walked paths did not intersect the strongest zero-dose hotspots, so a single walk cannot be relied on to locate the places that matter most. Even with sensible refinements to reduce bias, the method is constrained by corridor dependence, small sample size, and ambiguity about the bounds of inference.

At best, RCM may be acceptable as a purely operational tool for mop-up activities: walking, identifying unvaccinated children encountered, and facilitating immediate referral or vaccination. The intended user in that case is health facility staff working within a small, well-defined catchment area where the walked corridor can plausibly cover the population of interest — not program managers seeking representative estimates for higher administrative levels. But under the implementation tested here (a single walk to a 20-child quota), it is not well-suited to support any statement about the catchment area beyond the narrow corridor actually traversed.

5.0.4.6 NSUM

NSUM is theoretically appealing as a way to extract more information per respondent by leveraging social network reports. In Kano, however, the results suggest that core NSUM assumptions were strained. The most likely explanation is transmission error: respondents often could not reliably report the vaccination status of contacts’ children, and the visibility-factor correction appeared to overcorrect, yielding estimates that diverged from the gold standard without settling into a stable, calibratable bias. A second factor may be barrier effects: respondents’ named alters may not be representative of households more broadly, so the alter distribution can systematically differ from the population distribution in ways that are not easily repaired.

Even setting those sources of bias aside, the expected efficiency gains were limited by network scale. The effective network denominator was only about 11 eligible alters per respondent. That is far below the large alter networks (often 100+) where NSUM tends to deliver its biggest payoff. In other words, even under optimistic assumptions, NSUM might still offer some informational advantage over a direct probability sample per interview, but the magnitude of that advantage would likely be modest in this setting simply because the observed networks were small. In short, NSUM is not a viable approach to immunization coverage estimation in the foreseeable future: the conditions it depends on — alters whose vaccination status is reliably visible to respondents, and personal networks large and representative enough to deliver real efficiency gains — are not features of immunization that look likely to change in the populations where coverage measurement is most needed. We therefore do not recommend NSUM as a substitute for probability-based coverage measurement.

5.0.5 Conclusions and Recommendations

5.0.5.1 Overall Assessment

The gold-standard multistage cluster coverage survey and LQAS strike the most defensible balance between statistical rigor and operational feasibility. Both are probability-based designs with controlled error, and they serve complementary objectives: the gold standard provides precise benchmark prevalence estimates; LQAS provides rapid, ward-level pass/fail classification for supervisory decisions. Used together, they support both strategic planning and routine program monitoring.

AS occupies a narrower position than the within-design gains alone suggested. The non-sentinel field implementation supports feasibility and within-design gains. The sentinel simulation is more relevant for choosing between AS and conventional PPS: AS can outperform conventional sampling when zero-dose children are spatially clustered enough for the adaptive step to exploit, as seen in parts of the Nassarawa simulation grid. Across the sentinel simulation as a whole, however, the gains were modest and uneven once AS was compared against a same-total-budget conventional PPS sample. The method also requires advanced statistical capacity in the field and a more complex operational workflow. For routine zero-dose measurement, those costs will often outweigh the expected gain unless prior data, pilot work, or strong contextual knowledge point to useful spatial clustering.

ARR and NSUM are not recommended for zero-dose prevalence estimation. Both methods showed unstable bias relative to the gold standard, and neither produced estimates that could serve as reliable benchmarks for program planning. We do not see a clear path forward for either method in this context.

RCM is a distinct case. While it is not suitable as a general-purpose coverage estimator under the implementation tested here, it has promise for hyper-local assessment provided that the catchment area is clearly defined and that mild methodological adjustments are made (for example, tighter specification of the inferential area to the walked corridor, and recognition that serial autocorrelation along the route reduces effective sample size). Under the current single-walk, 20-child-quota implementation, RCM occupies a narrow legitimate niche for operational mop-up activities, but is unlikely to be representative of the catchment area it is intended to represent unless this area is very small or unless more random walks are added. Even then, a sample size of 20 children — while potentially sufficient for coverage classification — would generally still be considered too noisy for coverage point estimation. Implementation choices vary substantially across organizations, even when they use the same method name. Differences in sampling discipline, supervision, and quality-assurance practice can materially change both statistical performance and practical cost footprint. Method comparisons should therefore be interpreted as comparisons of implemented designs, not only nominal method labels.

5.0.5.2 Cost and Time Implications

The time-motion findings show that labor is the dominant resource input across methods. Fieldwork contributes most person-time, but analysis and technical review are major financial drivers because they are concentrated among higher-cost specialists. For budgeting, this means total financial cost cannot be reduced substantially without either narrowing analytic scope or reducing analytic capacity.

Marginal field costs per additional unit are more similar across methods than total costs. Large total-cost differences are driven mainly by sample size, fixed overhead, and implementation scope. For planning, method choice is therefore less about a simple low-cost versus high-cost dichotomy and more about matching a method’s full cost structure to the required inferential precision.

A related implication is that sample-size reduction is a bounded lever for total cost. Because planning, supervision, analysis, and technical review do not scale linearly with sample size — and, in the Kano cost structure, are concentrated in higher-priced specialist time while enumerator labor is comparatively inexpensive — halving sample size does not come close to halving total cost. The precision-versus-cost tradeoff is also asymmetric along the precision curve. At the small-sample end, modest upward adjustments yield outsized precision gains — moving from 20 to 40 children, for instance, halves the variance and cuts the standard error by about 29% (a factor of \(1/\sqrt{2}\)) before design effects — so the productive direction of movement for rapid designs is upward, not downward. At very large sample sizes, by contrast, the precision loss from modest reductions is small, but the cost savings are also modest because specialist overhead dominates. In settings where field labor is expensive relative to specialist time, the balance shifts and sample-size reduction regains more of its force. A productive reframe, then, is right-sizing: growing very small samples where a modest boost yields outsized precision gains, and trimming very large samples where resources are constrained — rather than treating uniform sample-size reduction as the primary cost lever.

Implementation quality also drives both time and cost. Disciplined probability-based execution requires callbacks, revisits, supervision, and documentation, which increase workload but protect validity. Comparisons across implementers should therefore be interpreted as comparisons of both price and rigor, not price alone.

5.0.5.3 A Path Toward Model-Assisted Probability Sampling

Beyond method selection, this study points to a practical opportunity: integrating open-source geospatial data into probability survey design and implementation. Two gains are available.

The first is sampling efficiency: Nigeria Demographic and Health Survey (NDHS)-derived modeled coverage surfaces and building footprint datasets can stratify clusters before sampling, concentrating effort in areas likely to contain zero-dose children. Model-assisted stratification reduces sampling variance without introducing bias, since estimates remain design-based with appropriate weights.

The second is operational efficiency: georeferenced building footprint data enable sampling designs that approximate simple random sampling without multi-stage cluster selection and household listing. GPS-verified building assignments and geofencing create a cleaner audit trail and reduce implementation drift — the silent bias source visible in this study’s RCM results.

Together, these advances support a tiered measurement strategy that places probability sampling at the center but deploys it more intelligently:

• Invest in periodic probability surveys to establish and refresh coverage benchmarks, using adaptive variants only when prior evidence suggests enough spatial clustering to justify the added complexity.
• Use LQAS for routine supervisory classification at the ward or supervision area level.
• Use model-assisted stratification and building footprint sampling to improve efficiency and implementation fidelity.
• Use existing free resources such as the NDHS modeled surfaces to estimate zero-dose prevalence at the LGA level when no data is otherwise available. While this information may not be recent (e.g., dating back to 2018), it can still provide a useful prevalence estimate when no other information is available at that level of granularity. In this study, the 2018 NDHS modeled surface agreed with the 2025 gold-standard LGA estimates within roughly 7 percentage points on average (mean absolute difference; Intraclass Correlation Coefficient (ICC) 0.73 across 15 Kano LGAs; see Figure 3.19 and Table 3.28).

Concrete methodological and Monitoring and Evaluation (M&E) recommendations are set out in Chapter 6. Endline and impact-measurement design — including the recommended pre-post structure, timing, age cohort, indicator definition, and sampling implications — is treated in the baseline report (Mindset 2025).

Mindset. 2025. “Kano Zero-Dose Baseline Survey Report.” https://zd25.netlify.app/.