12  Optimal Visit Placement

Prerequisites: Chapters 5, 8, and 11.

12.1 Learning objectives

By the end of this chapter you should be able to:

• Explain why the timing of measurements, holding their number fixed, affects the precision of a treatment-by-time interaction.
• State how the optimal placement depends on the covariance structure, and give the optimum under compound symmetry, AR(1), and random slopes with measurement error.
• Compare equally spaced and clustered designs by simulation.
• Recognize when the theoretical optimum should not be adopted, and why.

12.2 Orientation

A longitudinal trial has to decide how many times to measure each patient and when. The number is usually debated; the timing is usually not, and defaults to equal spacing for administrative convenience. Equal spacing is almost never optimal.

The reason is visible in the simplest case. If the treatment effect is a difference in linear slopes, the estimate of a slope from a set of observations has variance inversely proportional to the sum of squared deviations of the observation times from their mean. That sum is maximized, for a fixed number of observations in a fixed window, by placing half at each end. Under a pure measurement-error model, the optimal design for estimating a slope difference is to put everything at the two endpoints and nothing in between.

Real trials do not do this, for reasons that are partly statistical (the covariance structure is not pure measurement error, and interim measurements protect against dropout and detect non-linearity) and partly not (patients need clinical visits; safety must be monitored). The chapter’s purpose is to make the trade-off explicit, so that departures from the optimum are chosen rather than inherited.

12.3 Provenance

The simulation results in this chapter come from the research compendium 05-optimal-visit-placement (project visitplacement), which compares equally spaced and clustered designs for a two-group trial with linearly divergent treatment effects under a random-intercept, random-slope, independent-residual data-generating model. The report is at analysis/report/report.Rmd.

12.4 The statistician’s contribution

(Judgment 1.) Which covariance structure the data actually have. The optimal design under compound symmetry differs from the optimum under AR(1), which differs from the optimum under random slopes with measurement error. Choosing a design from the wrong structure can produce a worse trial than equal spacing. The structure must come from prior longitudinal data.

(Judgment 2.) How much interior information to buy as insurance. A design placing all observations at the endpoints is optimal for estimating a linear slope difference and provides no way to check whether the trajectory is linear, no protection against dropout before the final cluster, and no interim data for monitoring. Interior observations are insurance, and the premium should be paid consciously.

(Judgment 3.) Whether the endpoint is really a slope. If the estimand is the mean difference at a single landmark visit rather than a difference in rates, the optimality calculus changes entirely, and the visits that matter are the ones at and near the landmark.

12.5 The theory

Consider \(n\) patients per arm, each measured at times \(t_1, \dots, t_J\) within \([0, T]\), with a linear divergence in means and a covariance structure to be specified. The quantity of interest is the treatment-by-time interaction \(\delta\).

Compound symmetry. All pairs of observations on a patient share correlation \(\rho\), and there is no patient-specific slope. The patient-level random intercept is differenced out of any contrast, so what remains behaves like independent noise for the purpose of slope estimation, and precision is proportional to \(\sum_j (t_j - \bar t)^2\). The optimum places half the observations at \(t = 0\) and half at \(t = T\). Winkens et al. (2005) show that efficiency improves by clustering measurements near the ends, and in this structure specifically near the end where the treatment effect is largest.

AR(1). Correlation decays with the gap between observations. Observations close together are nearly redundant. Two measurements, at baseline and at the end, are already highly efficient; additional observations placed between them add little because they are strongly correlated with their neighbors.

AR(1) plus measurement error, or random slopes plus independent error. This is the realistic case, and the optimum depends on the parameter values. Clustering is still favored, but not to the degenerate two-point extreme, because independent measurement error at each occasion means that replicate observations at the same time point do carry additional information.

The general lesson is that the covariance structure determines the design, and that results derived under one structure do not transfer. This is the compendium’s second stated conclusion, and it is worth stating in a design meeting whenever someone cites a rule of thumb.

12.6 The simulation comparison

The compendium compares two designs with the same number of patients and the same number of visits, differing only in timing: equal spacing across the study window, and a clustered design concentrating observations near the boundaries. The data-generating model has a random intercept, a random slope, and independent homoscedastic residuals, which combines features of compound symmetry (through the intercept) and of measurement error (through the residual).

library(nlme)

simulate_design <- function(times, n_per_arm = 100,
                            delta = 0.5,
                            sd_int = 1.0, sd_slope = 0.3,
                            sd_resid = 0.5, n_sim = 2000) {
  J <- length(times)
  ests <- replicate(n_sim, {
    id  <- rep(seq_len(2 * n_per_arm), each = J)
    arm <- rep(rep(0:1, each = n_per_arm), each = J)
    tt  <- rep(times, times = 2 * n_per_arm)
    b0  <- rnorm(2 * n_per_arm, 0, sd_int)[id]
    b1  <- rnorm(2 * n_per_arm, 0, sd_slope)[id]
    y   <- b0 + (b1 + delta * arm) * tt +
           rnorm(length(tt), 0, sd_resid)
    fit <- lme(y ~ tt * arm, random = ~ tt | id,
               control = lmeControl(opt = 'optim'))
    fixef(fit)['tt:arm']
  })
  c(mean = mean(ests), sd = sd(ests))
}

equal     <- seq(0, 1, length.out = 5)
clustered <- c(0, 0, 0.5, 1, 1)

simulate_design(equal)
#>   mean     sd
#> 0.4991 0.0731
simulate_design(clustered)
#>   mean     sd
#> 0.5004 0.0625

Both designs are unbiased, as they must be. The clustered design has a smaller empirical standard error, here by about 15%, which corresponds to a sample-size reduction of roughly 27% for the same power. The compendium reports this comparison across parameter values with the standard ADEMP performance measures, and finds the direction consistent with the theory while the magnitude depends strongly on the ratio of slope variance to residual variance, exactly as in Chapter 11.

NoteCheck your understanding: why the interior visits are not free

Question. If clustering at the endpoints is more efficient, why does any trial place visits in the middle?

Answer.

Four reasons, three of them good.

Dropout. A patient who withdraws at month 12 of an 18-month trial contributes nothing to a design whose only post-baseline cluster is at month 18. In an equally spaced design they contribute several observations that inform their slope. Under realistic dropout the efficiency ranking can reverse, and the compendium lists this as its first limitation: the comparison assumes complete data.

Model checking. A two-point design fits a straight line to two points and cannot detect curvature. If the trajectory is not linear, the estimand itself is mis-specified and no amount of efficiency helps.

Safety and clinical necessity. Patients on an investigational drug need to be seen. Visits scheduled for safety can carry the efficacy measure at low marginal cost.

Convention. The fourth reason, and the bad one. Equal spacing is the default because it is the default.

The practical resolution is a compromise design: retain the safety visits, but weight the efficacy measurements toward the ends, taking duplicate or triplicate measurements at baseline and at the final visit rather than adding interior occasions. Duplicates at the ends reduce measurement error exactly where the design is most sensitive to it, and they cost a single extra administration of the instrument rather than an extra clinic visit.

12.7 Design criteria

The compendium follows the optimal-design literature in distinguishing criteria.

D-optimality minimizes the determinant of the covariance matrix of all parameter estimates. Appropriate when several parameters matter.

Ds- or c-optimality targets a single parameter or contrast, which for a trial is usually the treatment-by-time interaction. This is the criterion that matches the trial’s actual objective.

Cost-constrained optimality minimizes variance subject to a budget in which patients and visits have different prices. This is the criterion that matches the trial’s actual constraint, and it usually recommends fewer visits on more patients than an unconstrained criterion would, because the marginal value of the fifth visit is small relative to the marginal value of another patient.

Maximin designs (as in Ouwens et al., 2002) optimize the worst case over a range of plausible parameter values, which is the appropriate response to the fact that the covariance parameters are not known at design time. This is the honest criterion for practice, and it is the one least often used.

12.8 What number of measurements

A separate question from placement, and the answer is usually ‘fewer than you think’. Once the design has observations at both ends of the window, additional interior observations add information at a sharply diminishing rate, because they are correlated with the ones already present. Analyses of the number of repeated measures in this literature typically find that three to five well-placed occasions capture most of the achievable precision for a linear trend, and that further occasions are better spent on more patients.

The exception is when dropout is substantial, in which case additional occasions are insurance rather than information, and when non-linearity is expected, in which case the number of occasions is set by the number of parameters in the trajectory model plus enough to check its fit.

12.9 Worked example: choosing visits for a 24-month trial

A trial in a slowly progressive disease, 24-month follow-up, endpoint the annual rate of change on a continuous scale. Prior data: slope SD 0.28 per year, residual SD 0.55, intercept SD 1.4. Dropout historically 18% by 24 months, roughly uniform.

Candidate designs, all with five efficacy assessments:

• A: equal spacing at 0, 6, 12, 18, 24 months.
• B: clustered at 0, 0, 12, 24, 24 (duplicates at ends).
• C: endpoints only at 0, 0, 0, 24, 24, 24 with six assessments, for comparison.
• D: 0, 0, 6, 18, 24, 24.

Complete-data comparison by simulation. Relative efficiency for the treatment-by-time interaction, taking A as the reference: B is 1.24, C is 1.31, D is 1.21.

With 18% dropout, uniform over the window. B falls to 1.11, C falls to 0.94, D holds at 1.14. The endpoints-only design is now worse than equal spacing, because every dropout before month 24 contributes only baseline data and hence nothing about their slope. Design D, which retains interior observations at months 6 and 18, is the most robust.

Decision. Design D. It captures most of the clustering gain, retains interior information as dropout insurance, permits a check of linearity, and coincides with visits the protocol needs for safety anyway.

Reporting. The protocol states the visit schedule, the efficiency rationale, and the dropout assumption under which the schedule was chosen. If the observed dropout exceeds the assumption, the design’s efficiency claim weakens, which the SAP should acknowledge.

12.10 Collaborating with an LLM on design timing

Prompt 1: ‘What is the optimal visit schedule for this longitudinal trial?’

What to watch for. Models will usually recommend clustering at the endpoints, citing the sum-of-squares argument, without asking about the covariance structure or dropout. The recommendation is right in the model it assumes and can be wrong in yours.

Verification. Simulate the candidate schedules under your covariance structure and your dropout pattern before adopting any of them.

Prompt 2: ‘Simulate a comparison of these visit schedules.’

What to watch for. Simulation code that generates data under one covariance structure and fits a model assuming another, which conflates design comparison with model misspecification. Also check that dropout, if included, is generated the way you intend.

Verification. Confirm the fitted model recovers the generating parameters when the design is the reference one.

Prompt 3: ‘How many measurement occasions do we need?’

What to watch for. An answer without a cost model. The number of occasions is a budget question, and the right comparison is against spending the same money on patients.

Verification. Compute the variance per dollar for several combinations of \(n\) and \(J\), using your actual per-patient and per-visit costs.

12.11 Principle in use

1. Choose the timing deliberately. Equal spacing is a choice; it should be made rather than inherited.

2. Simulate under dropout before adopting an optimal design. Optimality results derived under complete data can invert when dropout is realistic, and dropout is always realistic.

3. Prefer duplicate measurements at the ends over extra interior visits. They buy most of the clustering gain at a fraction of the operational cost.

12.12 Exercises

1. Show that for a fixed number of observations in \([0, T]\) with independent errors, \(\sum_j (t_j - \bar t)^2\) is maximized by splitting the observations between the endpoints.

2. Repeat the simulation in this chapter with an AR(1) residual structure instead of independent errors. How does the relative efficiency of the clustered design change?

3. Add dropout to the simulation, with 20% of patients withdrawing at a uniformly distributed time. Compare designs A through D and reproduce the reversal described in the worked example.

4. Formulate the cost-constrained problem: minimize \(\mathrm{Var}(\hat\delta)\) subject to \(c_p n + c_v n J \le B\). Solve numerically for \(c_p = 20{,}000\), \(c_v = 900\), and \(B = 10\) million.

5. Construct a maximin design over slope-to-residual variance ratios from 0.1 to 1.0, and compare it to the design optimal at the midpoint of that range.

12.13 Further reading

• The compendium 05-optimal-visit-placement.
• Winkens et al. (2005), on optimal time points for linearly divergent treatment effects, and Winkens et al. (2006), on the optimal number of repeated measures and group sizes. These are the foundational references for the chapter.
• Ouwens et al. (2002), on maximin D-optimal designs when the covariance parameters are uncertain.
• Frost et al. (2008), for the interaction between visit placement and run-in observations.
• Harrall et al. (2023), a tutorial that works through power for longitudinal mixed models with attention to the measurement schedule.
• Fitzmaurice et al. (2011), Chapter 20, on design.
• The longpower package (Iddi & Donohue, 2022) and the optimal-design literature implemented in OptimalDesign.

Fitzmaurice, G. M., Laird, N. M., & Ware, J. H. (2011). Applied longitudinal analysis (2nd ed.). Wiley.

Frost, C., Kenward, M. G., & Fox, N. C. (2008). Optimizing the design of clinical trials where the outcome is a rate: Can estimating a baseline rate in a run-in period increase efficiency? Statistics in Medicine, 27(19), 3717–3731.

Harrall, K. K., Muller, K. E., Starling, A. P., Adgate, J. L., Dabelea, D., & Magzamen, S. (2023). Power and sample size analysis for longitudinal mixed models of health in populations exposed to environmental contaminants: A tutorial. BMC Medical Research Methodology, 23.

Iddi, S., & Donohue, M. C. (2022). Power and sample size for longitudinal models in R: The longpower package and Shiny app. The R Journal, 14(1), 264–282.

Ouwens, M. J. N. M., Tan, F. E. S., & Berger, M. P. F. (2002). Maximin D-optimal designs for longitudinal mixed effects models. Biometrics, 58(4), 735–741.

Winkens, B., Schouten, H. J. A., Breukelen, G. J. P. van, & Berger, M. P. F. (2005). Optimal time-points in clinical trials with linearly divergent treatment effects. Statistics in Medicine, 24(24), 3743–3756.

Winkens, B., Schouten, H. J. A., Breukelen, G. J. P. van, & Berger, M. P. F. (2006). Optimal number of repeated measures and group sizes in clinical trials with linearly divergent treatment effects. Contemporary Clinical Trials, 27(1), 57–69.