Comparative Effectiveness/Implementation of TB Case Finding in Rural South Africa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Effectiveness/Implementation of TB Case Finding in Rural South Africa (NCT02808507), a randomized na study. The primary outcome is Treatment Initiation Ratio in Facility Versus Contact Investigation Clinics.

2. Clinical Question

The broader study purpose was to compare approaches to finding TB cases in a rural Sub-Saharan African setting, considering case identification as well as the costs and feasibility of implementation. The primary endpoint addressed a narrower operational question: the relative rate of treatment initiation associated with facility-based screening versus contact investigation. This distinction matters. A comparison of treatment initiation is not itself a direct comparison of every case-finding, cost, or implementation outcome named in the study description.

The record describes three broad strategies: screening people attending primary care clinics, investigating household contacts of newly diagnosed TB cases, and using incentives to promote contact screening. The primary comparison groups facility-based screening against contact investigation clinics. A separate secondary outcome compares household-based and incentive-based contact tracing. These are related questions, but they do not estimate the same contrast or use the same outcome.

3. Trial Design

The registry describes a randomized, parallel-group study with no masking. The study enrolled 4852 participants and is listed as completed. The condition is tuberculosis, and the intervention is named active TB case finding. The recorded phase is NA.

The facility-based strategy was to be implemented at clinics in that arm for 18 months. Study staff were to encourage providers to screen consenting patients attending the clinics, regardless of the original reason for the visit. The contact screening arm contained household-based and incentive-based sub-arms. The record’s descriptions of those sub-arms are incomplete, so further procedural detail is not reported in the registry record.

The primary outcome is described over 18 months and compares facility-level treatment-initiation rates between facility-based screening and contact investigation clinics. Its population is a subgroup of the total study population: the record lists 1929 participants in the facility-based arm and 1726 participants in the contact screening arm for this outcome. Those figures describe participants, not the numbers of treatment initiations.

The study summary says investigators also planned to assess the number of cases identified, cost-effectiveness, and implementation feasibility. The listed secondary outcomes include secondary TB cases identified, costs of household contact investigation strategies, estimated costs per contact screened, cost per secondary case identified, and an incremental cost-effectiveness ratio. Numerical results for most of those outcomes are not reported in the registry record.

The registry gives a start date of 2016-07-18 and a primary completion date of 2018-01-17. Separately, the primary outcome population description refers to an intervention period beginning July 18,2015 and ending January 17, 2018. The start-date difference is not resolved in the registry record. The record does not report the allocation sequence or concealment procedures.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The population for this outcome consists of a sub-group of the total study population (those enrolled during the intervention period of July 18,2015 - January 17, 2018). All participants from the facility-based screening arm are included (n=1929), and the participants of the contact screening arm (n=1726) are included (this is a combination from the household-based and incentive-based screening arms).

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Treatment Initiation Ratio in Facility Versus Contact Investigation Clinics, measured over 18 months.

The primary endpoint is titled the treatment initiation ratio in facility versus contact investigation clinics. Its description states that the primary analysis compared facility-level rates of treatment initiation, first using an unadjusted ratio and then an adjusted analysis. The outcome is therefore intended to express a relative rate between the two strategies, rather than simply the number of participants enrolled in each arm.

Treatment initiation is a programmatically relevant endpoint because it reflects a step after case finding: identifying people who proceed to treatment. A case-finding strategy might identify people without necessarily producing the same pattern of treatment initiation, so the endpoint captures a different part of the service pathway than case identification alone. The registry summary also identifies case counts, costs, and implementation feasibility as study interests, but those are not interchangeable with the primary treatment-initiation comparison.

The registry lists participant counts for the primary outcome population, but it does not give the treatment-initiation event counts or the facility-level denominators underlying the reported rate ratio. The participant counts should not be read as treatment initiations. Consequently, the sponsor’s reported rate-ratio analysis is the interpretable primary result; the arm-level participant counts alone do not permit an independent reconstruction of that endpoint.

7. Results Posted in the Registry

• Contact Screening: 100.0% (1726/1726) versus 100.0% (1929/1929) on control; risk difference 0.0 percentage points (95% CI 0.0 to 0.0), risk ratio 1.00 (1.00–1.00); unadjusted two-proportion z-test p = n/a.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Comparative Number of Secondary TB Cases Identified in Incentive-based Versus Household-based Contact Tracing

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Contact Tracing Incentive-based Sub-arm: 1.1% (17/1510) versus 1.2% (17/1413) on control; risk difference -0.1 percentage points (95% CI -0.9 to 0.7), risk ratio 0.94 (0.48–1.83); unadjusted two-proportion z-test p = 0.846.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Contact Tracing Incentive-based Sub-arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry names secondary outcomes spanning case identification, contact-screening costs, cost per contact screened, cost per secondary case, and incremental cost-effectiveness. The available numerical secondary result concerns secondary TB cases identified in household-based versus incentive-based contact tracing. Numerical findings for the other listed secondary outcomes are not reported in the registry record, so the overall pattern across those outcomes cannot be assessed from the posted results.

The available contact-tracing result is centered near no difference, while its interval allows a broad range of relative effects. This is an uncertain secondary comparison, not evidence that the sub-arms are interchangeable. It also addresses a different endpoint and contrast from the primary analysis. The primary outcome compares facility-based screening with contact investigation clinics on treatment initiation; the secondary result compares two contact-tracing sub-arms on secondary cases identified. Their estimates need not move together because they concern different strategies, populations, and stages of the case-finding process.

Secondary results generally carry less weight than a prespecified primary result when they are among several outcomes, especially when the analysis plan and multiplicity procedures are not reported. Testing or interpreting many outcomes can increase the chance that an apparently notable result occurs by chance. In general, adjustment for multiplicity or a clearly stated outcome hierarchy can help readers understand how confirmatory the secondary analyses are. Neither a multiplicity procedure nor a prespecified hierarchy is reported in the registry record.

The study description says cost-effectiveness and feasibility were of interest, but the record does not provide enough numerical secondary findings to evaluate those questions. The posted secondary evidence should therefore be read as incomplete rather than as a comprehensive account of all additional outcomes. It can add context to the primary result, but it cannot establish the study’s broader economic or implementation conclusions.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Comparative Number of Secondary TB Cases Identified in Incentive-based Versus Household-based Contact Tracing
• Total Cost of Household Contact Investigation Strategies
• Estimated Costs Per Contact Person Screened in the Household-based and Incentive-based Contact Investigation Arms
• Cost Per Secondary Case of TB Identified Among Contacts, Per Arm
• Incremental Cost-effectiveness Ratio

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome description identifies a facility-level rate-ratio analysis. A rate ratio compares the rate in one group with the rate in another. A value of 1 represents equal rates on that ratio scale; values on either side represent a relative difference. The registry reports the ratio for facility-based screening versus contact investigation clinics as 1.04. The analysis is based on clinic-level counts and covariates, not simply the participant totals listed for the outcome population.

The record describes a two-stage adjustment. In the first stage, a Poisson regression is fitted to facility-level counts using district and historical-volume covariates, irrespective of study arm. The historical-volume variable is described as the annual number of people started on TB. A Poisson model is commonly used for count outcomes; in general, it relates expected counts to explanatory variables. The record then describes residual ratios, calculated as observed counts divided by expected counts, as inputs to the second stage. That stage estimates the between-arm rate ratio and its confidence interval.

In general, adjustment for district and historical volume can account for measured differences in facility context that might otherwise affect a comparison. It does not guarantee that all sources of confounding have been removed. The record says the adjustment addressed residual confounding by those specified factors. It does not report additional covariates, model diagnostics, or a fuller account of assumptions, so those should not be inferred.

The registry also describes an unadjusted ratio as the first step of the primary analysis, but it does not post a separate numerical estimate for that step in the results. Arm-level participant totals cannot substitute for the facility-level outcome counts or denominators. The comparison fields list the participant values as equal to their group denominators, producing a zero risk difference and p=1.0. Those values do not encode treatment initiations and are not a valid recalculation of the primary endpoint. The reported facility-level analysis is the relevant result.

The secondary comparison of secondary TB cases is presented with counts by contact-tracing sub-arm and a reported Poisson-regression prevalence ratio. A prevalence ratio compares the prevalence in one group with that in another; a value of 1 indicates equal prevalence on that scale. The record also contains an unadjusted risk-difference comparison. These are distinct measures: a risk difference expresses an absolute contrast, while a ratio expresses a relative contrast. In general, relative and absolute measures answer complementary questions, and the absolute difference can appear small when the underlying event frequency is low.

The registry includes planning illustrations based on the observed secondary-outcome effect. Such illustrations are not observed power and do not describe the trial’s original design justification. The record states that the illustrations assume a two-sided significance level of 0.05, equal allocation, and a normal approximation, with scenarios detecting a stated fraction of the observed effect. It does not report that these assumptions were used to plan the actual trial or that the original sample-size justification is available.

For the secondary endpoint, the record reports a 95% confidence interval for the prevalence ratio and a p-value from the sponsor analysis. A confidence interval describes a range of estimates reasonably compatible with the data and method, under the model’s assumptions. In general, wider intervals indicate less precision. A p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions; it is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect.

The registry lists 7 outcome measures and 3 analyses, and five secondary outcomes are indicated as posted. Numerical secondary results are not reported in the registry record for most of the listed cost and implementation outcomes. The record does not report a multiplicity adjustment across outcomes, a prespecified hierarchy for secondary analyses, or a complete statistical analysis plan. Those omissions limit how strongly isolated secondary findings can be interpreted.

11. Confidence Intervals and Precision

The primary estimate is 1.04, with a 95% confidence interval from 0.80 to 1.3. This interval includes 1, the value corresponding to equal rates on the ratio scale. It also spans estimates below and above 1, so the data do not pinpoint a single direction of difference. The reported p-value is 0.73, which is consistent with substantial uncertainty about whether the rates differ under the analysis used.

Precision is not the same as statistical significance. The point estimate gives one best estimate under the reported method, while the confidence interval conveys how much uncertainty surrounds it. Because the interval is not tightly concentrated around the point estimate, the result should not be read as demonstrating equivalence or ruling out potentially relevant differences. The registry does not state an equivalence margin or a non-inferiority margin.

The secondary prevalence-ratio interval runs from 0.51 to 1.95, with a reported point estimate of 1.0. It includes 1 and allows a wide range of relative associations. This is imprecise evidence about the contact-tracing comparison, rather than evidence that the approaches have exactly the same outcome. The secondary unadjusted risk-difference interval also spans zero. The two measures provide different views of uncertainty and should not be conflated.

The sample-size illustrations attached to the secondary comparison are planning scenarios based on fractions of its observed effect. They do not show the trial’s observed power, and they do not replace the confidence interval as a description of precision. The registry does not report a precision target or sample-size justification for the primary endpoint. Missing event counts and facility-level denominators also prevent readers from independently checking the primary estimate’s precision from the participant totals alone.

12. Analyses Reported by the Sponsor

The registry’s reported primary analysis gives a treatment-initiation ratio of 1.04, a 95% confidence interval from 0.80 to 1.3, and p=0.73. Its outcome description says the analysis used facility-level rates, with adjustment for district stratification and historical annual numbers of people started on TB through a two-stage approach.

The arm-level comparison fields list participant values that match the participant denominators, yielding a risk difference of 0 and p=1.0. These fields do not provide treatment-initiation event counts or the facility-level rates described for the primary analysis. They therefore cannot serve as an independent, unadjusted reconstruction of the treatment-initiation ratio. The sponsor’s reported analysis is the interpretable primary result in the registry record; the discrepancy flag is not marked true.

The secondary endpoint has a separate sponsor-reported Poisson-regression prevalence ratio of 1.0, with a 95% confidence interval from 0.51 to 1.95 and p=0.80. The registry also includes an unadjusted risk-difference calculation for that endpoint. The measures and analyses should be kept distinct: the sponsor’s prevalence-ratio analysis is not the primary facility-level treatment-initiation comparison, and the unadjusted secondary calculation is not a replacement for it.

Further details that would allow a more complete audit, including event counts, facility-level denominators, model diagnostics, and missing-data handling, are not reported in the registry record.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures and secondary comparisons, including case identification and several cost outcomes. It does not report whether the investigators adjusted for multiple comparisons, used a prespecified hierarchy for outcomes, or treated the secondary analyses as exploratory. Without that information, isolated secondary p-values should be interpreted cautiously. In general, examining multiple outcomes creates more opportunities for a chance finding, even when each individual test uses a conventional threshold.

The record describes the primary population as a subgroup of the total study population enrolled during the intervention period. It lists 1929 participants in the facility-based screening arm and 1726 in the contact screening arm. The record does not provide a full account of the analysis population beyond that description, such as whether all randomized participants were analyzed according to their original assignment or how eligibility for the primary subgroup was determined. Those details are not reported in the registry record.

Missing-data procedures are not reported in the registry record. The primary outcome description does not explain how missing facility-level counts, incomplete outcome ascertainment, or other unavailable data were handled. The record also does not describe sensitivity analyses for missing data. This limits assessment of whether the reported estimate could depend on assumptions about unavailable observations.

The registry gives a two-stage description of adjustment for district and historical volume in the primary analysis. However, a full statistical analysis plan, model diagnostics, and details of any interim analyses are not reported in the registry record. No interim analysis should be assumed. Likewise, the sample-size planning illustrations for the secondary outcome are not evidence of the original trial’s sample-size justification or observed power.

The primary outcome population description gives an intervention-period start date of July 18,2015, whereas the registry’s study start date is 2016-07-18. The record does not explain the difference. This ambiguity affects the chronology readers can reconstruct from the registry, although it does not change the reported primary estimate itself.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry lists zero serious adverse events and zero other adverse events in the risk sets shown for the facility-based screening arm, the household-based contact-tracing sub-arm, and the incentive-based contact-tracing sub-arm. It also lists zero deaths in each of those groups. These figures describe the registry’s reported safety entries; they should not be treated as proof that no adverse events occurred in every participant or that safety was assessed identically across all strategies.

The record does not list serious adverse-event terms. It also does not provide narrative detail about event definitions, ascertainment procedures, duration of safety follow-up, or how missing safety information was handled. The figures therefore offer limited information about safety beyond the counts entered in the registry. They do not support a comparison of risks with precision, and they should not be used to infer that an intervention is free of harm.

Safety results are separate from the case-finding and treatment-initiation outcomes. A zero entry in a registry safety field does not indicate whether a strategy identified TB cases or led to treatment initiation. Those questions are addressed by different outcomes, with their own limitations.

15. What the Result Does, and Does Not, Mean

The primary result describes an estimated facility-level treatment-initiation ratio of 1.04 for facility-based screening versus contact investigation clinics. Its 95% confidence interval runs from 0.80 to 1.3, and the reported p-value is 0.73. The estimate does not show a statistically clear difference under the reported analysis, but it does not prove that the strategies have identical rates. The interval leaves uncertainty about the size and direction of the relative difference.

The result applies to the primary comparison and outcome described in the registry. It is not a direct estimate of the number of TB cases found, the proportion of all participants who began treatment, or the comparative cost-effectiveness of the strategies. The secondary contact-tracing comparison concerns a different outcome and different pair of approaches. It cannot be used as a substitute for the primary treatment-initiation analysis.

The posted data do not establish that either strategy is superior, equivalent, or ineffective. A non-significant result is not proof of no effect. Equivalence would require a defined margin and an analysis designed to assess whether the plausible differences fall within that margin; such information is not reported in the registry record.

The study’s stated interests include costs and implementation feasibility, but numerical results for most of those outcomes are not reported in the registry record. The primary result alone cannot answer whether one strategy is more affordable, easier to implement, or more effective at identifying cases. Those broader conclusions would require the relevant outcome results and sufficient detail about how they were measured and analyzed.

The findings should also be understood in light of the reported population and analysis. The primary outcome uses a subgroup of the full study population and a facility-level rate-ratio method. Participant counts alone do not reconstruct that result. The registry does not report several details needed for a full independent audit, including primary event counts, facility-level denominators, missing-data handling, and a complete statistical analysis plan.

16. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between the reach of a case-finding strategy and the outcomes that follow. Screening clinic attendees, investigating household contacts, and encouraging contact screening through incentives are related approaches, but they operate through different pathways. Treatment initiation, case identification, cost, and feasibility are separate outcomes. Keeping them separate prevents a result on one measure from being generalized to every aspect of the intervention.

The primary analysis is also a reminder that the unit and scale of an analysis matter. The registry describes a facility-level rate ratio adjusted for district and historical volume. The participant totals reported for the outcome population are not a substitute for facility-level event counts or denominators. An apparent calculation based on participant totals would answer a different, and in this case unsupported, question.

Uncertainty is central to interpretation. The reported primary interval includes the equal-rate value, but it also covers relative differences on both sides of that value. The secondary interval is broad as well. These results illustrate why a point estimate or p-value alone is insufficient: intervals help communicate the range of effects that remain compatible with the data and method.

Finally, the registry’s broad study aims extend beyond the numerical results available for interpretation. Its listed cost and implementation outcomes could be important for understanding how strategies perform in practice, yet their numerical findings are not reported in the registry record. The distinction between a study’s intended scope and the outcomes available to evaluate is important when assessing what the evidence can support.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry’s primary result cannot be independently reconstructed from the participant counts. It does not report treatment-initiation event counts or the facility-level denominators used in the rate-ratio analysis. The comparison fields instead contain participant values matching their denominators; those fields do not represent the primary endpoint and should not be read as an outcome re-analysis.

The intervention descriptions are incomplete. In particular, the recorded descriptions of the contact-screening sub-arms are truncated, limiting the ability to understand exactly how household and incentive approaches were carried out. Although the record names 28 clinics in the facility-based arm description, comparable implementation details for the contact arm are not available in full.

The registry’s study start date is 2016-07-18, while the primary outcome population description gives an intervention-period start date of July 18,2015. The record does not explain this difference. The relationship between those dates should not be inferred.

The registry does not report missing-data handling, model diagnostics, a full statistical analysis plan, or whether secondary comparisons were adjusted for multiplicity. It also does not report numerical results for most listed cost and implementation outcomes. These limitations restrict independent verification and leave the broader economic and operational questions unanswered in the posted results.

The secondary case-identification comparison has an interval that permits a broad range of relative effects. The planning illustrations based on that observed effect are not a substitute for precision in the observed result, and they do not establish the original design rationale or observed power. Finally, the registry’s zero safety entries come without detailed ascertainment or follow-up information, so they are limited evidence about adverse events rather than a comprehensive safety assessment.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Comparative Effectiveness/Implementation of TB Case Finding in Rural South Africa — NCT02808507.
• Registry record last updated 2024-09-05; status last verified 2024-08.
• Results first posted 2022-12-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT02808507 is a completed randomized, parallel-group study of active TB case finding in rural South Africa, sponsored by Johns Hopkins Bloomberg School of Public Health. The registry lists no masking, phase NA, enrollment of 4852, a study start date of 2016-07-18, and primary completion on 2018-01-17.

The primary endpoint compares facility-level treatment-initiation rates between facility-based screening and contact investigation clinics over 18 months. The reported ratio is 1.04, with a 95% confidence interval from 0.80 to 1.3 and p=0.73. The registry also reports a secondary comparison of secondary TB cases identified in household-based versus incentive-based contact tracing, but numerical results for most listed secondary cost and implementation outcomes are not reported in the registry record.

The result should be interpreted as uncertain evidence about the specified primary comparison, not as proof of equivalence or a conclusion about all case-finding, cost, feasibility, or safety outcomes. Important analysis details, including missing-data handling and multiplicity procedures, are not reported in the registry record.