Increasing power and robustness in screening trials by testing stored specimens in the control arm Authors: Hormuzd A. Katki, Li C. Cheung Published: 2026 ABSTRACT BackgroundScreening trials require large sample sizes and long time-horizons to demonstrate mortality reductions. We recently proposed increasing statistical power by testing stored control-arm specimens, called the “Intended Effect” (IE) design. The IE design increases power by increasing the effect size via restricting analysis to only those people in both arms who are affected by screening, namely, those who test-positive. Hence the design requires storing control-arm specimens for future testing. To evaluate feasibility of the IE design, the US National Cancer Institute (NCI) is collecting blood specimens in the control-arm of the NCI Vanguard Multicancer Detection pilot feasibility trial. However, key assumptions of the IE design require more investigation and relaxation.MethodsWe relax the IE design to (1) reduce costs by testing only a stratified sample of control-arm specimens by incorporating inverse-probability sampling weights, (2) correct for potential loss-of-signal in stored control-arm specimens, and (3) correct for non-compliance with control-arm specimen collections. We also examine sensitivity to “unintended effects” of screening (i.e. outcome rates in screen-negatives increasing due to false reassurance).ResultsIn simulations, testing all primary-outcome control-arm specimens and a 50% sample of the rest maintains nearly all the power of the IE while only testing half the control-arm specimens. Power usually remains increased from the IE analysis (versus the standard analysis) even if unintended effects exist. The IE design is robust to some loss-of-signal scenarios, but otherwise requires retest-positive fractions that correct bias at a small loss of power. The IE can be biased and lose power under control-arm non-compliance scenarios, but corrections correct bias and can increase power.ConclusionsThe IE design can be made more cost-efficient and robust to loss-of-signal. Unintended effects will not typically reduce the power gain over the standard trial design. Non-compliance with control-arm specimen collections can cause bias and loss of power that can be mitigated by corrections. Although promising, practical experience with the IE design in screening trials is necessary.Supplementary InformationThe online version contains supplementary material available at https://doi.org/10.1186/s12874-026-02920-2. Introduction Randomized controlled trials (RCTs) for screening tests require large sample sizes and long time-horizons to demonstrate mortality reductions [1–3]. For example, the NHS-Galleri Multicancer Early Detection (MCED) screening trial randomized 140,000 people and requires 8–10 years to examine cancer mortality results [4]. MCED tests use a single blood specimen to screen for cancer at multiple organ sites simultaneously, including those without recommended screening, which is an exciting prospect [5, 6]. However, RCT data on the clinical benefits and harms of MCED-based screening will be unavailable for many years. Yet, in the US, MCED tests are already being sold, underscoring the need to provide RCT evidence as soon as possible [7]. To increase statistical power in screening trials, we [8] and others [9–14] have proposed testing stored material among controls and comparing trial outcomes only among those who ever test positive, which we call the “Intended Effect” (IE) design [8]. The intended effect of screening is that only those who test-positive at least once (“ever-positive”) could receive treatments which affect mortality. In contrast, those who never test-positive (“never-positive”) never undergo diagnostic procedures (much less treatment) and thus their mortality should be unaffected by screening. Thus, removing everyone who likely could not be affected by screening (i.e. removing never-positives), and comparing outcomes only among ever-positives in both arms, can have substantially greater statistical power [8]. An MCED RCT relying the IE design could halve the sample-size required to attain 90% power [8, 15]. To evaluate feasibility of the IE design, the US National Cancer Institute (NCI) is collecting blood specimens in the control-arm of the NCI Vanguard MCED pilot feasibility RCT [16]. Although promising, the IE design requires assumptions that have not been adequately investigated or relaxed. We relax the IE design to (1) reduce costs by testing only a stratified sample of control-arm specimens, (2) account for potential loss-of-signal in stored control-arm specimens, and (3) correct for non-compliance with control-arm specimen collections. We also examine sensitivity to “unintended effects” of screening (i.e. outcome rates in screen-negatives increasing due to false reassurance). Methods Brief review of the intended effect (IE) design/analysis Figure 1 shows a schematic of the IE analysis for an example idealized MCED trial. The standard trial analysis, with 50,000 individuals per-arm, 2% cancer death rate, and a screening relative risk (RR) of 0.90 would have only 65% power. The IE design tests control-arm specimens and removes everyone who are never test-positive, because they should not be affected by screening as they receive no medical interventions (i.e., assumed to have “no unintended effects”): in Fig. 1 their relative risk (”RRneg”) equals 1. The IE analysis focuses on the ever-positives, the only people who might receive medical interventions and thus benefit from screening. The RR among ever-positives is RRpos = 0.867, which is stronger than RR = 0.90. Importantly, the p-value for RRpos is tenfold smaller than for the RR. To achieve 90% power at α = 0.05, the standard trial would require 98,000 individuals per-arm versus 53,000 per arm for the IE design. Hence the IE analysis, which focuses on RRpos and its p-value, achieves 90% power at about half the sample-size required by the standard analysis.Fig. 1Schematic of the Intended Effect (IE) analysis. The standard trial analysis table is decomposed into 2 subtables of those who test negative on all screens in each arm, and those who test positive on at least one screen in each arm (note that this requires storing control-arm specimens for future testing). Because those who test negative on all screens never receive treatments, there is no intended effect of screening for the 95,000 screen-negatives and hence RRneg exactly equal 1. Removing them from the analysis leads to the increases in power shown in the Ever-positive table, which is the Intended Effect analysis Schematic of the Intended Effect (IE) analysis. The standard trial analysis table is decomposed into 2 subtables of those who test negative on all screens in each arm, and those who test positive on at least one screen in each arm (note that this requires storing control-arm specimens for future testing). Because those who test negative on all screens never receive treatments, there is no intended effect of screening for the 95,000 screen-negatives and hence RRneg exactly equal 1. Removing them from the analysis leads to the increases in power shown in the Ever-positive table, which is the Intended Effect analysis Secondarily, the IE analysis also calculates the risk difference and relative risk among never-positives (RDneg and RRneg, respectively) to test the “no unintended effects” assumption, which is that RDneg = 0 and RRneg = 1. See Supplement for more review and notation, and discussion of ethical issues [17, 18]. Extending the IE analysis to only test a stratified sample of control-arm specimens and effect on statistical power Rather than testing all control-arm specimens, it is more cost-efficient to test everyone who experiences the primary outcome (“cases”) and a stratified random sample of the others (“controls”) for testing. The Supplement shows how to use observed sampling fractions as inverse-probability weights (IPW) to estimate the RRpos. Stratified sampling of control-arm specimens achieves cost-efficiency by (1) ensuring that important subgroups are adequately represented to enhance generalizability of findings, and (2) reducing variability to improve precision. Stratification efficiently allocates testing towards those contributing most to testing positive: those who developed cancer or have risk-factors that predispose to cancer, such as age, race, sex, smoking history, or BMI. The more predictive the strata, the fewer controls require testing to achieve statistical power. Stratified sampling enhances cost-efficiency, statistical power and interpretability, making findings more robust and generalizable. Because stratified sampling only tests a subset of controls, some loss of statistical power is inevitable versus testing all controls. We simulate the IE design to calculate the power loss from different stratified sampling plans. Sensitivity of IE statistical power to unintended effects of screening The IE design assumes that individuals who never test positive receive no medical interventions and are unaffected by screening. The “no unintended effects” assumption is analogous to the “exclusion restriction” in causal inference, that “never-takers” in both arms should experience the same outcome rates [19]. However, there may be unintended effects of screening, such as false-reassurance in the screen-arm never-positives, who may skip standard of care (SOC) screens or otherwise alter their behavior to be riskier (RDneg < 0, or equivalently, RRneg > 1), and thus a negative screen inadvertently causes harm (in our notation, positive relative risks correspond to negative risk differences). The opposite of false-reassurance is ‘non-assurance’, which could happen if people in the screen arm who test never-positive are not reassured and seek out extra screening (RDneg > 0, or equivalently, RRneg < 1). Power is determined by α and the non-centrality parameter (see page 91 in [20]). The Supplement calculates the ratio increase in the non-centrality parameter for RDpos versus the standard RD, for any value of RDneg:\documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$${Z}_{ratio}=\left\{1-\frac{R{D}_{neg}}{RD}\cdot P\left(M-\right)\right\}\cdot \sqrt{\frac{P\left(M+\right)}{P\left(M+|D+\right)P\left(M+|D-\right)}} ,$$\end{document}where “RD” is the overall trial risk-difference, “P(M +)” is the probability of being ever-positive (i.e. testing positive on any screen), “P(M-)“ is the probability of testing never-positive, and “D + ” denotes experiencing the trial outcome (e.g. cancer death). The radical is > 1 because its numerator is a weighted average of the 2 factors in the denominator. Thus \documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$${Z}_{ratio}>1$$\end{document} and the IE analysis has more power than the standard analysis if there are no unintended effects (RDneg = 0) or if there is false-reassurance in the screen-arm (RDneg < 0). If there were ‘non-assurance’ (RDneg > 0), the IE analysis can still have more power than the standard analysis, although not guaranteed. Supplement explains how we simulated to calculate power for various scenarios. Correcting for loss-of-signal in stored control-arm specimens Stored specimens degrade over time. There may be less positivity by testing stored specimens (in the control arm) versus testing fresh specimens (in the screen arm), which may bias RRpos or RRneg. Degradation of stored specimens rarely (if ever) results in gain-of-signal, and we assume it is impossible. The Supplement demonstrates:If loss-of-signal is only differential by arm (i.e. non-differential by outcome), there is no bias in RRpos by substituting the observed ever-positivity as the true ever-positivity, although there is loss of power. An example of loss-of-signal only differential by arm is if the stored specimens that lose signal were a simple random sample of all ever-positives. If instead false positives were more likely to have a weak degradable signal than true positives, then loss-of-signal is differential by outcome and there is bias in RRpos.For RRneg, even if loss-of-signal is only differential by arm, there is bias by substituting the observed ever-positivity for true ever-positivity. If loss-of-signal is only differential by arm (i.e. non-differential by outcome), there is no bias in RRpos by substituting the observed ever-positivity as the true ever-positivity, although there is loss of power. An example of loss-of-signal only differential by arm is if the stored specimens that lose signal were a simple random sample of all ever-positives. If instead false positives were more likely to have a weak degradable signal than true positives, then loss-of-signal is differential by outcome and there is bias in RRpos. If loss-of-signal is only differential by arm (i.e. non-differential by outcome), there is no bias in RRpos by substituting the observed ever-positivity as the true ever-positivity, although there is loss of power. An example of loss-of-signal only differential by arm is if the stored specimens that lose signal were a simple random sample of all ever-positives. If instead false positives were more likely to have a weak degradable signal than true positives, then loss-of-signal is differential by outcome and there is bias in RRpos. For RRneg, even if loss-of-signal is only differential by arm, there is bias by substituting the observed ever-positivity for true ever-positivity. For RRneg, even if loss-of-signal is only differential by arm, there is bias by substituting the observed ever-positivity for true ever-positivity. To correct bias, we propose also storing a portion of the specimen in the screen-arm (screen-arm conducts testing on fresh specimens) and retest all stored specimens that tested positive on the fresh specimen. Define \documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$$\widetilde{M}$$\end{document} as the observed ever-positivity indicator, which degrades the true M by loss-of-signal. For simplicity, assume no gain-of-signal is possible. We estimate (1) the fraction of the screen-arm true-positives that also retest-positive (\documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$${P}_{1}\left(\widetilde{M}+|M+,D+\right)$$\end{document}), and (2) the fraction of the screen-arm false-positives that also retest-positive (\documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$${P}_{1}\left(\widetilde{M}+|M+,D-\right)$$\end{document}). These fractions account for the possibility that there may be more loss of signal in false-positives, which may tend to be weaker signals than true-positives. We substitute retest-positivity to unbiasedly calculate the outcome rate in control-arm ever-positives:\documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$${P}_{0}\left(D+|M+\right)={\left\{1+\frac{{P}_{0}\left(D-\right)}{{P}_{0}\left(D+\right)}\times \frac{{P}_{0}\left(\widetilde{M}+|D-\right)/{P}_{1}\left(\widetilde{M}+|M+,D-\right)}{{P}_{0}\left(\widetilde{M}+|D+\right)/{P}_{1}\left(\widetilde{M}+|M+,D+\right)}\right\}}^{-1},$$\end{document}and thereby correct bias in RRpos. See Supplement for derivation and demonstration of bias correction. A similar calculation to correct bias in RRneg is in the Supplement. Correcting for non-compliance with specimen collections in the control-arm We focus on non-compliance in the control-arm from skipping specimen collections (we assume the screening test cannot be obtained outside of the trial, which is a problem for the standard analysis as well). Hence non-compliance can only reduce ever-positivity. Note that, those who skipped screens but tested positive at any screen they attended, are known to be ever-positive. Thus we examine robustness to including those who both skipped screens and never tested positive at any screen they attended (i.e. those with unknown ever-positivity), into the never-positive table. In this framework, non-compliance to specimen collections is mathematically equivalent to a particularly acute loss-of-signal. Thus, the results from robustness to loss-of-signal section carry-over. Thus, just as loss-of-signal that is only differential by arm (i.e. non-differential by outcome) does not cause bias, similarly non-compliance that is only differential by arm does not cause bias (although there is loss of power). Similarly, just as loss-of-signal that is differential by outcome causes bias, non-compliance that is differential by outcome also causes bias. See Supplement for more discussion. Correcting for control-arm non-compliance requires placing everyone in both arms with unknown ever-positivity into a third 2 × 2 table (see Supplement). We do not correct estimates to perfect compliance in both arms, because perfect compliance is unrealistic. We propose that the non-compliance correction be to set the non-compliance pattern in the control-arm to equal that in the screen-arm. That is, we propose to not correct for non-compliance in the screen-arm. This is because it is appropriate to “penalize” screening if the screening test is difficult for participants to adhere to. Non-compliance that is completely non-differential cannot cause bias. Simulations to quantify bias and power to examine impact on statistical testing We conducted simulations to quantify reduction in bias and loss of power by relaxing the various assumptions (see Supplement for details). We develop and evaluate 95% CI coverage from using a bootstrap variance estimator. All computations were done in R 4.3.0. All code is available on GitHub (hkatki/intended-effect-analysis). Results Efficient stratified sampling of stored control-arm specimens to test Table 1 simulated sampling of control-arm specimens with binomial sampling among those who develop a trial outcome and a single fraction of those who do not develop trial outcome. When sampling all controls for testing provides 89–90% power, sampling half of the controls for testing provides 84–86% power (Table 1A), nearly the same power while obviating testing for half the control-arm. If only 80% of cases could be tested (Table 1B), power drops from 89–90% to 87–88% when sampling 70% of the controls along with the 80% of cases, showing that small losses in testing of cases could be made up by testing more controls. The simulations do not include other sampling strata predictive of ever-positivity, such as cancer-status, age, or other risk-factors, which would make the sampling plan even more efficient.Table 1A/B Power for estimating RRpos by subsampling a fraction of non-events in the control arm for testing all of their stored specimens (all control-arm participants who experience a trial outcome have all their stored specimens tested). Parameters for 3 situations set so that sampling everyone yields 90% power: 5% chance of ever testing positive, 2% event rate, 50% of the total participants are in the control arm, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), and no loss-of-signal from testing stored specimens(A) Sample 100% of events in the control arm for testing of all their stored specimens, and a fraction of the non-events in the control arm for testing of all their stored specimensNon-event sampling fractionPowern = 100,000n = 75,000n = 50,000RRpos = 0.867RRpos = 0.8RRpos = 0.70.10.540.640.670.20.710.770.800.30.780.810.840.40.810.850.850.50.840.860.860.60.840.870.870.70.860.880.880.80.860.880.880.90.870.890.8810.890.900.90B) Sample 80% of events in the control arm for testing of all their stored specimens, and a fraction of the non-events in the control arm for testing of all their stored specimensNon-event sampling fractionPowern = 100,000n = 75,000n = 50,000RRpos = 0.867RRpos = 0.8RRpos = 0.70.10.520.620.660.20.700.740.760.30.770.790.810.40.810.820.830.50.830.830.840.60.850.850.850.70.860.850.850.80.870.870.850.90.880.870.8510.870.870.86 Table 1A/B Power for estimating RRpos by subsampling a fraction of non-events in the control arm for testing all of their stored specimens (all control-arm participants who experience a trial outcome have all their stored specimens tested). Parameters for 3 situations set so that sampling everyone yields 90% power: 5% chance of ever testing positive, 2% event rate, 50% of the total participants are in the control arm, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), and no loss-of-signal from testing stored specimens(A) Sample 100% of events in the control arm for testing of all their stored specimens, and a fraction of the non-events in the control arm for testing of all their stored specimensNon-event sampling fractionPowern = 100,000n = 75,000n = 50,000RRpos = 0.867RRpos = 0.8RRpos = 0.70.10.540.640.670.20.710.770.800.30.780.810.840.40.810.850.850.50.840.860.860.60.840.870.870.70.860.880.880.80.860.880.880.90.870.890.8810.890.900.90B) Sample 80% of events in the control arm for testing of all their stored specimens, and a fraction of the non-events in the control arm for testing of all their stored specimensNon-event sampling fractionPowern = 100,000n = 75,000n = 50,000RRpos = 0.867RRpos = 0.8RRpos = 0.70.10.520.620.660.20.700.740.760.30.770.790.810.40.810.820.830.50.830.830.840.60.850.850.850.70.860.850.850.80.870.870.850.90.880.870.8510.870.870.86 A/B Power for estimating RRpos by subsampling a fraction of non-events in the control arm for testing all of their stored specimens (all control-arm participants who experience a trial outcome have all their stored specimens tested). Parameters for 3 situations set so that sampling everyone yields 90% power: 5% chance of ever testing positive, 2% event rate, 50% of the total participants are in the control arm, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), and no loss-of-signal from testing stored specimens Unintended effects and statistical power in the IE analysis The Supplement demonstrates that the IE analysis has more power than the standard analysis if there are no unintended effects (RDneg = 0, or equivalently, RRneg = 1) or if there is false-reassurance in the screen-arm (RDneg < 0). But even if there were ‘non-assurance’ (RDneg > 0), the IE analysis can still have more power than the standard analysis. Figure 2 plots power versus RRpos for an example MCED trial with RR = 0.9, as ever-positivity and RRneg = 1vary. The standard analysis has only 36% power, but many IE analyses achieve > 90% power as RRpos becomes smaller and as ever-positivity decreases. As expected, the power gain is greatest for false-reassurance (RRneg = 1.05), then no intended effects (RRneg = 1), and least gain for non-assurance (RRneg = 0.95).Fig. 2Fixing overall trial RR = 0.9 and 2% control-arm outcome prevalence, IE analysis power as a function of RRpos (from 0.5 to 0.9) and ever-positivity (2.5%, 5%, 50%, 90%), for no unintended effects (RRneg = 1; left), false-reassurance (RRneg = 1.05; middle), and non-assurance (RRneg = 0.95; right). The standard analysis has 36% power (solid black line in all 3 plots). Y-axis is on the probit scale. Horizontal dotted lines denote 80% and 90% power Fixing overall trial RR = 0.9 and 2% control-arm outcome prevalence, IE analysis power as a function of RRpos (from 0.5 to 0.9) and ever-positivity (2.5%, 5%, 50%, 90%), for no unintended effects (RRneg = 1; left), false-reassurance (RRneg = 1.05; middle), and non-assurance (RRneg = 0.95; right). The standard analysis has 36% power (solid black line in all 3 plots). Y-axis is on the probit scale. Horizontal dotted lines denote 80% and 90% power The power curves are monotonic and similar for ever-positivity > 5%, and power is close to that of the standard analysis when RRpos = RR. However, for very small 2.5%−5% ever-positivity and RRpos ≈ RR, power is not monotonic at RRpos ≈ RR because the larger number of outcomes at RRpos ≈ RR can outweigh a stronger RRpos < RR (see Supplement Figure S1 for an example). Correcting for potential loss-of-signal from testing stored versus fresh specimens When loss-of-signal is non-differential by outcome, RRpos is unbiased with little loss in power at small loss-of-signal fractions of 10%, but substantial loss of power if 30% or more of signal were lost (Table 2A). However, RRneg = 1 is strongly biased even at small loss-of-signal with highly inflated type-1 error α (Table 2A). When loss-of-signal is differential by outcome (Table 2B), bias generally ensues. With a 20% loss-of-signal in non-events (and 10% in events), RRpos is substantially underestimated (0.867 to 0.80, a non-conservative bias).Table 2A/B/C Sensitivity to, and correcting for, loss-of-signal from testing stored specimens that are truly positive. All situations set: total trial n = 100,000 (50,000 in each arm), 5% chance of ever testing positive, 2% event rate, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), RRpos = 0.867, and testing 95% of control-arm stored specimens who experience a trial outcome and testing 50% of control-arm stored specimens who do not experience a trial outcome(A) Non-differential loss-of-signal (i.e. equal loss-of-signal fraction from testing stored specimens from those who experience a trial outcome versus those who do not). RRpos is not biased by non-differential loss-of-signal, with little loss in power at small loss-of-signal fractions of 10%. RRneg is strongly biased even at 10% loss-of-signal with highly inflated type-1 error αloss of signalmean RRposmean RRnegpower for RRposα for RRneg50%0.8670.410.66140%0.8670.470.72130%0.8670.540.75120%0.8670.630.80110%0.8670.780.820.860%0.8671.000.840.053(B) Differential loss-of-signal such that there is more loss-of-signal from testing stored specimens from controls who do not experience a trial outcome versus controls who do experience the trial outcome. With just a 10% loss-of-signal in non-events (and 0% in events), RRpos is underestimated (0.867 vs 0.81), a non-conservative bias. If there is loss-of-signal in events, RRneg is strongly biased even at 10% loss-of-signal in events, with highly inflated type-1 error αloss of signaleventsnon-eventsmean RRposmean RRnegpower for RRposα for RRneg50%60%0.750.411140%50%0.770.471130%40%0.780.541120%30%0.790.631110%20%0.800.7810.840%10%0.811.010.990.0480%0%0.8671.000.840.053(C) Fixing differential loss-of-signal by storing a portion of specimen in the screen-arm, retesting all stored specimens for those ever screen-positive in the screen-arm, estimating retest-positive fractions among those who experienced the trial event (and did not), and using the retest-positive fractions to correct RRpos and RRneg estimates. RRpos and RRneg estimates are unbiased. Testing for \documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$$R{R}_{neg}$$\end{document} has proper type-1 error α. RRpos estimation loses some power if loss-of-signal is 10% in events and 20% in non-events (power drops from 0.84 to 0.79)loss of signaleventsnon-eventsmean RRposmean RRnegpower for RRposα for RRneg50%60%0.871.000.530.05140%50%0.871.000.590.04930%40%0.871.000.670.05120%30%0.871.000.730.04910%20%0.871.000.790.0520%10%0.871.000.820.0480%0%0.871.000.840.053 Table 2A/B/C Sensitivity to, and correcting for, loss-of-signal from testing stored specimens that are truly positive. All situations set: total trial n = 100,000 (50,000 in each arm), 5% chance of ever testing positive, 2% event rate, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), RRpos = 0.867, and testing 95% of control-arm stored specimens who experience a trial outcome and testing 50% of control-arm stored specimens who do not experience a trial outcome(A) Non-differential loss-of-signal (i.e. equal loss-of-signal fraction from testing stored specimens from those who experience a trial outcome versus those who do not). RRpos is not biased by non-differential loss-of-signal, with little loss in power at small loss-of-signal fractions of 10%. RRneg is strongly biased even at 10% loss-of-signal with highly inflated type-1 error αloss of signalmean RRposmean RRnegpower for RRposα for RRneg50%0.8670.410.66140%0.8670.470.72130%0.8670.540.75120%0.8670.630.80110%0.8670.780.820.860%0.8671.000.840.053(B) Differential loss-of-signal such that there is more loss-of-signal from testing stored specimens from controls who do not experience a trial outcome versus controls who do experience the trial outcome. With just a 10% loss-of-signal in non-events (and 0% in events), RRpos is underestimated (0.867 vs 0.81), a non-conservative bias. If there is loss-of-signal in events, RRneg is strongly biased even at 10% loss-of-signal in events, with highly inflated type-1 error αloss of signaleventsnon-eventsmean RRposmean RRnegpower for RRposα for RRneg50%60%0.750.411140%50%0.770.471130%40%0.780.541120%30%0.790.631110%20%0.800.7810.840%10%0.811.010.990.0480%0%0.8671.000.840.053(C) Fixing differential loss-of-signal by storing a portion of specimen in the screen-arm, retesting all stored specimens for those ever screen-positive in the screen-arm, estimating retest-positive fractions among those who experienced the trial event (and did not), and using the retest-positive fractions to correct RRpos and RRneg estimates. RRpos and RRneg estimates are unbiased. Testing for \documentclass[12pt]{minimal} \usepackage{amsmath} \usepackage{wasysym} \usepackage{amsfonts} \usepackage{amssymb} \usepackage{amsbsy} \usepackage{mathrsfs} \usepackage{upgreek} \setlength{\oddsidemargin}{-69pt} \begin{document}$$R{R}_{neg}$$\end{document} has proper type-1 error α. RRpos estimation loses some power if loss-of-signal is 10% in events and 20% in non-events (power drops from 0.84 to 0.79)loss of signaleventsnon-eventsmean RRposmean RRnegpower for RRposα for RRneg50%60%0.871.000.530.05140%50%0.871.000.590.04930%40%0.871.000.670.05120%30%0.871.000.730.04910%20%0.871.000.790.0520%10%0.871.000.820.0480%0%0.871.000.840.053 A/B/C Sensitivity to, and correcting for, loss-of-signal from testing stored specimens that are truly positive. All situations set: total trial n = 100,000 (50,000 in each arm), 5% chance of ever testing positive, 2% event rate, overall RR=0.9, RRneg = 1 (i.e. no false-reassurance), RRpos = 0.867, and testing 95% of control-arm stored specimens who experience a trial outcome and testing 50% of control-arm stored specimens who do not experience a trial outcome Table 2C shows that our proposed corrections to RRpos and RRneg = 1 by using stored samples in the screen-arm are unbiased and testing for RRneg = 1 (which is null) has proper type-1 error α. However, RRpos estimation inevitably loses power, e.g. if loss-of-signal is 10% in events and 20% in non-events, then power drops from 0.84 to 0.79. Correcting for non-compliance to specimen collections in the control-arm Figure S2 shows an example of correcting for arm-differential non-compliance, where the observed and corrected RRpos equal that under perfect compliance. Figure S3 shows an example of correcting for non-compliance that is differential by both arm and outcome, and the corrected RRpos no longer equals that under perfect compliance. This is because outcome-differential non-compliance implies that ever-positivity will be imbalanced between arms (except at the null of RR = 1, RRpos = 1, and RRneg = 1). See Supplement for more explanation about the figures. Table 3 shows simulation results from various non-compliance scenarios. Neither RRpos nor RRneg has bias under non-compliance that is non-differential, or differential by arm-only. However, power for RRpos is reduced from 88% to 74–77%. The non-compliance correction to RRpos increases power to 82–85%, showing that even if the correction is not needed to reduce bias, it can reduce variance and increase power.Table 3Simulating different non-compliance patterns to screening (screen arm) or blood collections (control arm) and calculating the mean RRpos and RRneg and power for RRpos, and correcting them for non-compliance. “D + ” denotes people who experience the trial primary outcome and “D- “ is otherwise. Non-compliance leads to a fraction of true ever-positives being observed as never-positive (first 4 columns). All other simulation parameters set as in Fig. 1. In simulations, corrected RRneg always maintained 5% type-1 errorNon-compliance among ever-positivesEver-positivityscreen arm D + screen arm D-control arm D + control arm D-control armscreen armmean RRposmean RRnegcorrected RRposcorrected RRnegpower for RRpospower for corrected RRposPerfect compliance0%0%0%0%5.0%5.0%0.8671.000.8671.0088%88%non-differential30%30%30%30%5.0%5.0%0.8671.010.8671.0174%82%differential by arm20%20%30%30%5.0%5.0%0.8671.010.8671.0177%83%differential by outcome30%10%30%10%4.69%4.73%0.8601.010.8601.0177%85%differential by outcome & arm30%15%15%30%5.30%4.78%0.5560.680.8611.01100%84%15%30%30%15%4.75%5.26%1.1481.480.8741.0175%84% Table 3Simulating different non-compliance patterns to screening (screen arm) or blood collections (control arm) and calculating the mean RRpos and RRneg and power for RRpos, and correcting them for non-compliance. “D + ” denotes people who experience the trial primary outcome and “D- “ is otherwise. Non-compliance leads to a fraction of true ever-positives being observed as never-positive (first 4 columns). All other simulation parameters set as in Fig. 1. In simulations, corrected RRneg always maintained 5% type-1 errorNon-compliance among ever-positivesEver-positivityscreen arm D + screen arm D-control arm D + control arm D-control armscreen armmean RRposmean RRnegcorrected RRposcorrected RRnegpower for RRpospower for corrected RRposPerfect compliance0%0%0%0%5.0%5.0%0.8671.000.8671.0088%88%non-differential30%30%30%30%5.0%5.0%0.8671.010.8671.0174%82%differential by arm20%20%30%30%5.0%5.0%0.8671.010.8671.0177%83%differential by outcome30%10%30%10%4.69%4.73%0.8601.010.8601.0177%85%differential by outcome & arm30%15%15%30%5.30%4.78%0.5560.680.8611.01100%84%15%30%30%15%4.75%5.26%1.1481.480.8741.0175%84% Simulating different non-compliance patterns to screening (screen arm) or blood collections (control arm) and calculating the mean RRpos and RRneg and power for RRpos, and correcting them for non-compliance. “D + ” denotes people who experience the trial primary outcome and “D- “ is otherwise. Non-compliance leads to a fraction of true ever-positives being observed as never-positive (first 4 columns). All other simulation parameters set as in Fig. 1. In simulations, corrected RRneg always maintained 5% type-1 error However, when non-compliance is differential by both arm and outcome in opposite directions (last 2 rows, Table 3), large bias ensues in the observed RRpos and RRneg. The corrections are necessary to remove bias, although note that outcome-differential non-compliance implies that the RRpos corrected to reflect the non-compliance pattern of the screen-arm will not equal the RRpos under perfect compliance. Power for RRpos remains high (84%) and corrected RRneg maintains 5% type-1 error. Performance of bootstrap standard error estimates for all corrections proposed Table S1 shows that the bootstrap accurately calculates the standard error for each correction and normal-approximation 95%CIs have nominal coverage. See Supplement for more details. Discussion We demonstrated that the IE design increases power versus the standard analysis of screening RCTs. However, the IE design requires assumptions that we relax and investigate sensitivity to. The IE design can be made more cost-efficient by testing only a stratified sample of control-arm specimens. Under false-reassurance, the power gain from the IE is even greater than if unintended effects did not exist. We demonstrate that the IE design is naturally robust to loss-of-signal that non-differential by outcome, and we make it robust to loss-of-signal that is differential by outcome by incorporating “retest-positive” fractions from the screen-arm. The IE is robust to non-compliance with control-arm specimen collections that is non-differential or differential by arm only, and non-compliance corrections can increase power. But if non-compliance is differential by both arm and outcome, bias ensues, and corrections must be used. The IE design reduces costs by requiring fewer participants to achieve 90% power, but increases costs by requiring testing of control-arm specimens. Recruiting a participant for screening RCTs in the US costs roughly $1000–5000, but a screening test (without markup) might cost $100–500 (roughly a factor of 10 less). Hence powering an RCT based on the IE design, which would reduce sample-size, may well have lower total cost than the standard design [13]. In this paper, we further improve cost-efficiency of the IE design by testing only a stratified sample of control-arm specimens. We found that at least half of control-arm specimens do not require testing to maintain nearly all the power. Our simulations did not include sampling strata likely associated with ever-positivity, such cancer-status, age or other risk-factors that would increase precision, cost-efficiency, and generalizability. Note that, if power gains from the IE are used to reduce sample-size, then trial investigators must be sure that non-assurance is impossible and must commit to the IE analysis as the primary analysis. We showed that even if unintended effects occur, the IE analysis still has substantially greater power than the standard analysis. However, the “no unintended effects” assumption can be tested whether RRneg equals 1, which is important to do. If the RRneg indicates substantial false-reassurance, that indicates that screening programs must emphasize to screen-negatives that they must continue to get standard-of-care screens and not change their behavior. We demonstrate that the IE design is robust to loss-of-signal that is differential only by arm. To account for loss-of-signal that is also differential by outcome, we extended the IE design to also store specimens in the screen-arm to calculate “retest-positive” fractions that are necessary to correct for bias. The only screen-arm stored-specimens that require testing are from those who test ever-positive, to examine whether their stored specimens “retest” ever-positive. For MCED tests, which are rarely positive, this would not appreciably increase testing costs. Because degradation of stored specimens rarely (if ever) results in “gain-of-signal”, we assumed it was not possible. If gain-of-signal were possible, then stored screen-arm specimens from never-positives would also have to be tested, which would increase testing costs. Testing only a stratified sample of the never-positives might suffice to correct bias. The IE design is robust to non-compliance with control-arm specimen collections that is non-differential or differential by arm only, but our corrections can increase statistical power. Non-compliance that is differential by both arm and outcome can cause serious bias in the uncorrected RRpos and RRneg. The corrections remove bias and power can be maintained. Conclusions The IE design is a promising approach to screening RCT design, but requires assumptions that we investigated and relaxed. Because the IE analysis, as we define it, has never been used, we need experience with the design and analysis, which will be obtained with the NCI Vanguard MCED pilot feasibility RCT.[16] If the IE analysis proves feasible and useful, a future large definitive randomized MCED screening trial could be powered for the IE analysis as the primary analysis, which would result in large cost savings versus the standard design and hence make the trial more feasible to conduct. Supplementary Information Supplementary Material 1. Supplementary Material 1.