Abstract
Objective.
Our lab previously showed in simulation that excluding the formal baseline from the eligibility window would reduce regression-to-the-mean (RTM), lower apparent placebo response, and improve antiseizure medication (ASM) trial efficiency. A recent software re-review revealed a reversal on the final point: excluding baseline worsened trial efficiency. We investigated this paradoxical finding further by comparing two otherwise identical designs that differed only in whether baseline contributed to eligibility.
Methods.
The calibrated seizure-diary simulator CHOCOLATES generated a shared pool of approximately 220,000 simulated candidates. In the Overlap design, the 3-month eligibility window included the 2-month formal baseline (3 prospective months total). In the Separate design, eligibility was determined during a 3-month qualification window; candidates meeting eligibility then completed a separate 2-month baseline (5 prospective months total). Eligibility thresholds were 3, 4, or 5 seizures/month. Placebo and proportional drug effects of 20%, 30%, and 40% were simulated. Endpoints were median percent change (MPC) and 50% responder rate (RR50). Empirical type I error was calibrated using 100,000 null trials per cell; sample size for 90% empirical power (N90) and prospective candidate-month burden were estimated.
Results.
Separate reduced baseline inflation (1.20 vs 1.60 seizures/month at the 4/month threshold), placebo MPC (−2.1% vs 6.7%), and placebo RR50 (12.1% vs 14.7%). However, Separate required more randomized participants in every scenario, increasing N90 by 5.7%−8.8% for MPC and 6.9%−17.9% for RR50. At the conventional 4/month threshold and 20% drug effect, RR50 required 620 randomized participants with Overlap versus 700 with Separate. Separate candidate-month burden was 1.32–1.45 times that of Overlap.
Significance.
Reducing RTM did not improve trial efficiency. The formal baseline both introduces RTM bias and verifies that randomized patients carry sufficient endpoint information; separating baseline from eligibility reduces the former but weakens the latter. In this simulation, the baseline-inclusive design was more efficient across every threshold, endpoint, and drug effect. Trial designers should evaluate eligibility and baseline rules as an integrated measurement system, not by apparent placebo response alone.
Keywords: epilepsy, antiseizure medication, randomized clinical trial, regression to the mean, placebo response, clinical trial design, simulation, sample size
1. Introduction
Across decades of antiseizure medication (ASM) trials, placebo arms have consistently reported substantial median percent reductions and fraction of 50%-responders, eroding observable drug effects, increasing required sample sizes, and perhaps contributing to recent failures of medications that appeared promising in earlier development [1–4].
A growing body of work indicates that much of this apparent placebo response is not a classical psychological placebo phenomenon. Big-data and simulation analyses suggest that natural fluctuation in seizure counts, combined with trial eligibility selection mechanisms, can reproduce the placebo-arm signal observed in historical ASM trials [5–8]. The relevant statistical phenomenon is regression-to-the-mean (RTM): when entry into a trial is conditioned on an observed seizure count being above some threshold, the subsequent observed count is expected to decline toward the patient-specific long-term mean even in the absence of any treatment effect [9].
The intuitive design fix is straightforward. If the same observation window is used for eligibility and for the baseline, the baseline is conditioned on being unusually high. The natural correction for this is to separate eligibility from baseline: that is, first qualify the patient in an upstream observation window, and then begin the baseline only after eligibility has been confirmed. In our own previous work, this baseline-separate design was proposed to reduce RTM and, by extension, to improve trial efficiency [10]. Recently, our lab discovered a calculation error in the simulation code. After correcting the error, we found trial efficiency worsened (rather than improved) in the baseline-separate case while the other results from that study remain intact: RTM does decrease when separating baseline from eligibility. The new efficacy result seemed counterintuitive. Rather than merely correcting the previous study simulation error, we wanted to drill deeper to understand why lowering RTM decreases trial efficiency. Therefore, rather than a mere correction to the original study, we wanted to broaden the lens and collect additional information to make things more interpretable.
To further explore this counterintuitive result, we used a realistic seizure-diary simulation to compare two designs that hold other elements constant except where the eligibility window sits relative to the baseline. We investigated the influence that separating baseline from eligibility has on RTM and on overall trial power.
2. Methods
2.1. Study design
This was an in silico (simulated) randomized-trial design study using a realistic seizure-diary generator (CHOCOLATES) developed and validated for drug-resistant epilepsy populations [11]. The study compared two qualification designs (“Overlap” and “Separate”) that share a single candidate pool, so differences between designs reflect timing and use of the baseline for eligibility (Figure 1). The structure of “Overlap” is nearly identical to a historical trial[12], while “Separate” has not been used before. In both cases, the same 2-month baseline was always used to determine the participant’s usual seizure rate. The goal was not to estimate efficacy of any specific drug, but to evaluate how the placement of the eligibility window relative to the baseline changes bias, statistical power, and operational burden. Full source code and analysis are available at https://github.com/GoldenholzLab/RTM-baseline.
Figure 1.
Separate and Overlap. Pictured here are the two ways being considered for determining eligibility, baseline and test periods. Both methods include 3 months of observation for eligibility, 2 months for baseline and 3 months for test, but the timing differs. The Overlap method is more typical of trials done in epilepsy and is faster, but conceptually, the Separate method is expected to produce less regression-to-the-mean.
2.2. Candidate pool and timeline
A shared pool of approximately 220,000 candidate diaries was simulated once and used within every design cell (each applying unique eligibility criteria). Within each cell, synthetic patients were randomly sampled. Each diary was aggregated into nine consecutive 30-day months indexed as: a burn-in month (M0), three pre-baseline months (P3, P2, P1), two baseline months (B1, B2), and three test months (T1, T2, T3). Eligibility thresholds were 3, 4, and 5 seizures/month. Prior work[10] found that as eligibility thresholds increased from 0 to 8 seizures/month, so did the fraction of RTM. We therefore elected to non-exhaustively explore values near the commonly employed 4/month eligibility in most modern adult ASM trials [3,4].
2.3. Qualification designs
Both designs applied the same 3-month seizure-frequency rule (total seizures over the 3-month eligibility window ≥ 3 × minSz). They differed only in which three months made up that window:
Overlap design: eligibility window = P1 + B1 + B2 (the 2-month baseline is part of eligibility; 3 prospective months total).
Separate design: eligibility window = P3 + P2 + P1; (eligibility failures completed 3 prospective months, whereas eligible candidates completed an additional 2-month baseline; 5 prospective months total).
Thus, the nominal duration of the eligibility rule was held constant, while the role of the baseline differed in each design.
2.4. Outcomes, statistical tests, and drug-effect model
Two efficacy endpoints were evaluated using standard methods[5–7,10,11,13]. Median percent change (MPC) was the patient-level percentage change in monthly seizure rate from the 2-month baseline (B1, B2) to the 3-month test period (T1,T2,T3), compared between arms by a two-sided Wilcoxon rank-sum test. The 50% responder rate (RR50) was the proportion of patients with ≥50% reduction from baseline to test, compared between arms by a two-sided Fisher exact test. Proportional drug effects of 0% (placebo), 20%, 30%, and 40% were applied to test-period seizure totals by binomial thinning, an approach that independently reduces each seizure probabilistically.
2.5. Power, type I error, and operational burden
Empirical type I error was calibrated using 100,000 null trials per cell. MPC required a calibrated alpha of 0.0485 to achieve a 0.05 nominal target; RR50 used 0.05 directly and remained conservative under both designs. N90 was defined as the total randomized sample size achieving 90% empirical power for the corresponding endpoint, threshold, drug effect, and design. The N90 search used 100,000 initial and 100,000 refinement replicates with isotonic regression[14] to enforce monotonicity of the empirical power curve. Additional calibration details, including empirical type I error tables, are reported in the Supplementary Appendix.
Operational burden was quantified in two ways: first, by the number of screened candidates required to yield the randomized N90 cohort (using the design-specific eligibility rate), and secondly, by determining the total candidate-months elapsed before randomization (screened candidates × prospective months pre-randomization, i.e., 3 for Overlap and 3 for disqualified Separate and 5 for qualified Separate).
2.6. Additional terminology
Every simulated patient had a “true” seizure frequency (meaning the underlying generator rate), which was subjected to many features like clustering, multi-day cycles, and certain types of random noise. “Baseline inflation” was defined as the amount by which the observed average frequency during the baseline months exceeded the ”true” frequency of each patient. “Apparent placebo response” was reported as placebo-arm MPC and placebo-arm RR50, calculated with the same procedure used for active arms. The term “placebo adjusted lift” here will be used to refer to the difference between placebo and drug outcome metrics, such as MPC lift or RR50 lift. The adjusted lift attempts to represent the “pure” effect of the drug after adjusting for the placebo response.
3. Results
3.1. Eligibility yield was nearly identical across designs
Both designs had essentially identical eligibility yields.. At thresholds of 3, 4, and 5 seizures/month, eligibility rates were approximately: 49.5% (for both), 40.9% (for both), and 34.2% (Separate), 34.3% (Overlap). Absolute eligible counts were 108,817 vs 108,911 at 3/month, 89,976 vs 89,946 at 4/month, and 75,438 vs 75,273 at 5/month for Overlap versus Separate.
3.2. Separate eligibility reduced RTM markers and apparent placebo response, as expected
Baseline inflation was lower under Separate at every eligibility threshold: 0.91 vs 1.21 seizures/month at 3/month, 1.20 vs 1.60 at 4/month, and 1.51 vs 2.06 at 5/month for Separate versus Overlap. Across thresholds, placebo-arm MPC values fell starting from 6.5%−7.4% under Overlap to between 0.0% and −2.6% under Separate. Analogously, across thresholds, placebo-arm RR50 values fell starting from 14.7%−15.1% to 12.1%−12.4% (Figure 2).
Figure 2.
Separate eligibility reduced RTM markers and apparent placebo response. At every threshold, the Separate design lowered baseline inflation, placebo median percent change, and placebo 50% responder rate. The expected RTM-reducing effect of separating eligibility from baseline was therefore reproduced cleanly.
3.3. Drug-arm response was lower under Separate, but placebo-adjusted response varied by endpoint
Across thresholds (3,4, and 5), in the representative 30% drug-effect scenario, the drug-arm signal was larger under Overlap (drug-arm MPC values were 33.3%−34.6% vs 28.5%−28.9%; drug-arm RR50 33.4%−33.7% vs 28.5%−29.1%). Because Overlap also produced higher placebo response, placebo-adjusted MPC lift was, in some specific cells, numerically larger under Separate (e.g., 30.7% vs 26.7% at the 4/month threshold), while placebo-adjusted RR50 lift was consistently larger under Overlap (e.g., 18.7% vs 16.4% at 4/month) (Figure 3).
Figure 3.
Drug-arm and placebo-adjusted response at a representative 30% proportional drug effect. Overlap produced larger raw drug-arm signals for both median percentage change (MPC) and 50%-responder rate (RR50). Note MPC is defined here such that positive values indicate reduction in seizures. Because Overlap also produced higher placebo response, placebo-adjusted median MPC lift could be larger under Separate, while placebo-adjusted RR50 lift was consistently larger under Overlap. Endpoint-specific variance and discreteness, not the median location shift alone, determined efficiency.
3.4. Type I error was controlled in both designs
After calibration, empirical type I error was tightly controlled (mean 4.79%−4.82% for MPC, 3.14%−3.33% for RR50, the latter remaining conservative under both designs). Detailed calibration values are reported in Supplementary Table S1.
3.5. Overlap required fewer randomized participants for 90% power
Across every threshold, endpoint, and drug-effect scenario, the Separate design required more randomized participants (i.e. placebo patients + drug patients) to reach 90% power, also known as N90(Figure 4). For MPC, the relative increase in N90 with Separate ranged from 5.7% to 8.8%. For RR50, the increase ranged 6.9%−17.9%. At the conventional 4/month threshold, MPC N90 for Overlap versus Separate was 328 vs 352 (20% drug effect), 132 vs 142 (30%), and 68 vs 72 (40%). RR50 was more punishing, with 620 vs 700 (20%), 234 vs 264 (30%), and 112 vs 124 (40%). Even in cells where the median placebo-adjusted MPC lift favored Separate, Separate still required more randomized participants for the same power.
Figure 4.
Randomized N90 by endpoint, threshold, and drug effect. Across every cell, the Separate design required more randomized participants to reach 90% power than the Overlap design. The penalty was modest but consistent for MPC and substantially larger for RR50.
3.6. Screening burden 32–45% higher under Separate
Across all simulated scenarios, Separate required 1.05–1.18 times as many screened candidates and 1.32–1.45 times as many candidate-months (Figure 5). At the 4/month threshold and 20% drug effect, the RR50 endpoint required 1,516 screened candidates and 4,548 candidate-months under Overlap versus 1,712 screened candidates and 6,536 candidate-months under Separate. In practical terms, the same trial would take approximately 32–45% greater pre-randomization observation burden to assemble for randomization under the design that reduces apparent placebo response.
Figure 5.
Prospective candidate-month burden. Because the Separate design requires 5 months of pre-randomization observation (3-month qualification + 2-month baseline) compared with 3 months under Overlap, candidate-month burden was 1.32–1.45-fold higher under Separate across every endpoint, threshold, and drug-effect scenario. The largest operational gap occurred for RR50 at low drug effects, the regime of greatest practical relevance for late-phase ASM development.
4. Discussion
The central finding of this simulation appears counterintuitive: the design that reduces RTM does not ultimately result in smaller trials. The Separate design behaved exactly as the standard RTM argument would predict. Baseline inflation fell. Placebo-arm MPC fell. Placebo-arm RR50 fell. And yet, despite these results, more randomized participants were required for 90% power across every threshold, endpoint, and drug effect tested. In the Separate design, the prospective time required to assemble each trial increased by 32%–45%. Evidently, RTM minimization is not the same problem as trial optimization.
4.1. Why does the intuitive design lose?
The baseline in an epilepsy trial has several jobs. In the Overlap case, it helps to select for higher seizure frequencies, producing RTM and apparent placebo improvement. This is the bias-introducing role. In both Overlap and Separate cases, the baseline is needed to normalize the treatment effect. When the baseline is low, small treatment effect variability will be amplified. This is the information-discarding role of the Separate case (Figure 6).
Figure 6.
The counterintuitive RTM result explained. The figure shows graphically why the Overlap case causes more RTM but also better trial efficiency, whereas Separate causes less RTM but less trial efficiency.
The MPC result is especially informative (Figure 3). Although the difference between drug and placebo was larger with the Separate construction, the efficacy was lower. The reason this happened relates to effect variability and per-patient information, not the change in effect magnitude. These mechanisms help explain why a design that “looks better” on placebo response can still be the more expensive design.
Of note, the fractions of eligible participants for the Separate vs. Overlap were nearly identical. Nearly the same numbers of participants were randomized. This is reasonable because in both cases 3 months were used to determine if criteria were met, with no other requirements yet attached. The difference arose in what happened next. In the Separate case, the baseline measurement was made after eligibility was already confirmed, whereas in the Overlap case, baseline was measured concurrently with the eligibility determination. The choice about randomization can be made as soon as a patient is deemed eligible, therefore in theory randomization can take place before baseline is measured in the Separate condition, but it cannot occur until baseline is measured in the Overlap condition.
Consistent with the findings in this study, Kerr et al. found that RTM-consistent response shifts in clinical ASM trials generally affected both treatment and placebo arms and therefore were not expected to reduce statistical power [15].
4.2. Reconciliation with prior work
Our previous report concluded that excluding baseline from eligibility reduces RTM and apparent placebo response and characterized this as an efficiency improvement [10]. The first part of that conclusion is replicated here. The second part is not. Of note, a software error was detected in the prior analysis which explains why the prior study suggested higher statistical power for the Separate condition. In the present analysis, the operationally relevant outcomes — randomized N90 and candidate-month burden — were uniformly worse under the baseline-separate design. We interpret the present results as a refinement: the earlier finding was correct about the mechanism but incorrect about the design recommendation, because it considered RTM in isolation rather than alongside endpoint information and prospective overall time required. The conventional baseline-inclusive design used in most modern adult ASM trials is, in this calibrated simulation, the more efficient choice.
4.3. Implications for trial design
Three implications follow. First, trial sponsors should be cautious about adopting a baseline-separate eligibility design solely on the argument that it reduces apparent placebo response. In our simulations, that reduction came at a 5%−18% penalty in randomized N and a 32%–45% increase in candidate-month burden. For real-world programs where recruitment is constrained, sites are limited, and timelines drive go/no-go decisions, those costs are substantial [3,4]. Adding a baseline-separate eligibility would also increase the time participants must wait until obtaining investigational treatment and likely increase dropout.
Second, the design space is wider than a binary choice between Overlap and Separate. Hybrid windows — for example, a short qualification window before a short baseline — may capture some of the RTM advantage without the full operational cost. These hybrid designs warrant further study. Time-to-event endpoints such as time to pre-randomization monthly seizure count (T-PSC) [16] use individualized baseline information rather than aggregate counts. These may interact differently with the bias-versus-information tradeoff identified here. With T-PSC, one might expect some very low baseline rates under the Separate configuration, which could cause additional problems[15]. Covariate adjustment for baseline rate, stratification or balancing of baseline rate during randomization, or other methods, may also recover some efficiency [13].
Third, the appropriate metric for “trial efficiency” is not placebo response or any single RTM marker in isolation. It is the joint cost of bias control, randomized sample size, and prospective candidate time. A design that wins on one and loses on the others is not necessarily an improved design.
4.4. Limitations
This is a simulation study, and its conclusions inherit the assumptions of the underlying generator and analysis pipeline. CHOCOLATES is calibrated to adult drug-resistant epilepsy. Results may not transfer to specialized sub-populations with substantially different seizure distributions or features [17], device trials, or studies of seizure freedom as an endpoint. Drug effect was applied as proportional thinning of test-period totals; effect models in which drug action depends on the individual baseline rate may interact differently with the two designs. Adherence, dropout, diary missing entries, and site-level effects were not addressed in the present work. Moreover, some of the results presented may differ from prospectively collected data due to financial incentives for trial enrollment in certain locales, differences between diary recall and real-time diary logging, and other real-life constraints. Additionally, although we used canonical 30-day months rather than the customary 28-day month, we do not think the results should be adversely affected. Finally, we evaluated only the canonical 3-month eligibility rule at 3/4/5 seizures per month; results at sharply different eligibility durations or thresholds may differ. Some studies require additional eligibility constraints designed to reduce seizure clustering (e.g. <21 seizure-free days); the impact of those constraints is outside the scope of the present work.
Despite these limitations, the direction of the finding was consistent across every threshold, endpoint, and drug effect tested. The Separate design never outperformed Overlap on N90 in any cell. We therefore interpret the qualitative conclusion — that minimizing RTM does not automatically minimize trial size — as robust within the population the simulator represents.
5. Conclusions
In simulated antiseizure medication trials, separating eligibility measurement from the baseline reduced regression-to-the-mean and apparent placebo response, as the standard argument predicts. It did not, however, reduce the number of randomized participants required to detect a treatment effect, and it significantly increased the prospective candidate time required to assemble each trial. The conventional baseline-inclusive design — the design used in most modern adult ASM trials — was the more efficient choice across every condition we evaluated. Epilepsy trial designers should not adopt baseline-separate eligibility on the assumption that lower apparent placebo response automatically purchases statistical or operational gain. Future work may uncover ways to reduce apparent placebo effects while simultaneously increasing trial efficiency.
Supplementary Material
HIGHLIGHTS.
Prior work suggested benefits from separating eligibility determination from baseline.
Making this separation reduces regression-to-the-mean (RTM) and lowers placebo rates.
This separation counterintuitively lowers trial efficiency.
Using the baseline to establish eligibility resulted in improved trial efficiency, even with higher placebo rates and higher RTM.
Acknowledgements and Funding
DG was funded by NIH K23NS124656, NIH R21NS142800 and ABPN. RB was funded by K23NS124656. OpenAI Codex was used to assist with coding and portions of manuscript preparation; however, the authors take full responsibility for the entire project including code, images, and manuscript.
Declaration of Interest
DMG has been provided speaker fees from Harvard Medical School, AAN, AES, ACNS, NNS, AI in Epilepsy and Neurology, Florida Epilepsy Alliance, and UT-Austin. He also previously has been a paid consultant for Neuro Event Labs, IDR, LivaNova, Health Advances, Duke University, Bloom Insights and Wiley. He has received grants from NIH, ABPN, BIDMC and the Lions Club. The other coauthors have no relevant conflicts to disclosure.
Footnotes
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Ethical Publication Statement
No new human participants were enrolled for this in silico study. The author confirms that the manuscript is consistent with the journal’s ethical publication principles. Because the analysis used only simulated data, institutional review board review was not required.
Data and Code Availability
All source code, analysis notebooks, and configuration files are publicly available at https://github.com/GoldenholzLab/RTM-baseline.
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Data Availability Statement
All source code, analysis notebooks, and configuration files are publicly available at https://github.com/GoldenholzLab/RTM-baseline.