# Optional stopping does not bias parameter estimates (if done correctly)

*tl;dr: Optional stopping does not bias parameter estimates from a frequentist point of view if all studies are reported (i.e., no publication bias exists) and effect sizes are appropriately meta-analytically weighted.*

- “… sequential testing appears to inflate the observed effect size”
- “discussion suggests to me that estimation is not straight forward?“
- “researchers who are interested in estimating population effect sizes should not use […] optional stopping“
- “we found that truncated RCTs provide biased estimates of effects on the outcome that precipitated early stopping” (Bassler et al., 2010)

**The good news is: if done correctly, optional stopping does not bias your effect size estimate at all, as I will demonstrate below.**

Given the recent discussion on optional stopping and Bayes, I wanted to solicit opinions on the following thought experiment.Researcher A collects tap water samples in a city, tests them for lead, and stops collecting data once a t-test comparing the mean lead level to a “safe” level is significant atp<.05. After this optional stopping, researcher A computes a Bayesian posterior (with weakly informative prior), and reports the median of the posterior as the best estimate of the lead level in the city.Researcher B collects the same amount of water samples but with a pre-specified N, and then also computes a Bayesian estimate.Researcher C collects water samples from every single household in the city (effectively collecting the whole population).Hopefully we can all agree that the best estimate of the mean lead level in the city is obtained by researcher C. But do you think that the estimate of researcher B is closer to the one from researcher C and should be preferred over the estimate of researcher A? What – if anything – does this tell us about optional stopping and its influence on Bayesian estimates?

Let’s simulate the scenario (R code provided below) with the following settings:

- The true lead level in the city has a mean of 3 with a SD of 2
- The “safe” lead level is defined at 2.7 (or below)

**Strategy A:**Start with a sample of n.min = 3, and increase by 1. After every increase, compute a one-sided t-test (expecting that the lead level is smaller than the safe level), and stop if

*p*< .05. Stop if you reach n.max of 50.

**Strategy B:**Collect a fixed-

*n*sample with the size of the final sample of strategy A. (This results in a collection of samples that have the same sizes as the samples from strategy A).

*not*compute a Bayesian posterior, because the usage of a prior

*will*bias the estimate. (A side note: When using a prior, this bias is deliberately accepted, because a small bias is traded in for a reduction in variance of the estimates, as extreme and implausible sample estimates are shrunken towards more realistic numbers). Here, we simply take the plain sample mean, because this is an unbiased estimator – at least in the typical textbook-case of fixed sample sizes. But what happens with optional stopping?

**A naive analysis**

*n*studies with the same sample sizes, we get a mean lead level of 3.00, which is exactly the true value.

**A valid analysis**

**If effect sizes from samples with different sample sizes are combined, they must be meta-analytically weighted according to their sample size (or precision).**Optional stopping (e.g., based on*p*-values, but also based on Bayes factors) leads to a conditional bias: If the study stops very early, the effect size must be overestimated (otherwise it wouldn’t have stopped with a significant*p*-value). But early stops have a small sample size, and in a meta-analysis, these extreme early stops will get a small weight.**The determination of sample size (fixed vs. optional stopping) and the presence of publication bias are separate issues.**By comparing strategy A and B, two issues are (at least implicitly) conflated: A does optional stopping*and*has publication bias, as she only reports the result if the study hits the threshold. Non-significant results go into the file drawer. B, in contrast, has a fixed sample size, and reports all results,*without*publication bias. You can do optional stopping without publication bias (stop if significant, but also report result if you didn’t hit the threshold before reaching n_max). Likewise, if B samples a fixed sample size, but only reports trials in which the effect size is close to a foregone conclusion, it will be very biased as well.

*under*estimations from late terminations (Schönbrodt, Wagenmakers, Zehetleitner, & Perugini, 2015). Hence, optional stopping leads to a

*conditional*bias (i.e., conditional on early or late termination), but it is

*unconditionally*unbiased.

- The strategies A and B
*without publication bias*report all outcomes - Strategy A
*with*publication bias reports only the studies, which are significantly lower than the safe lead level - Strategy B
*with*publication bias reports only studies which show a sample mean which is smaller than the safe lead level (regardless of significance)

### Some descriptive plots to illustrate the behavior of the strategies

*n*) is well-behaved and symmetric. The distribution from strategy A (optional stopping) shows a bump at small effect sizes (these are the early stops with a small lead level).

*n*design there is no conditional bias.

### The estimated mean levels

Here are the compute mean levels in our 8 combinations (true value = 3):

Sampling plan | PubBias | Naive mean | Weighted mean |
---|---|---|---|

sequential | FALSE | 2.85 | 3.00 |

fixed | FALSE | 3.00 | 3.00 |

sequential | TRUE | 1.42 | 1.71 |

fixed | TRUE | 2.46 | 2.55 |

**To summarize: (fixed sample size vs. optional stopping) and (publication bias or not) are orthogonal issues.**

*The only problem for biased estimates is the publication bias – not the optional stopping!*Concerning the sequential procedures described here, some authors have raised concerns that these procedures result in biased effect size estimates (e.g., Bassler et al., 2010, J. Kruschke, 2014). We believe these concerns are overstated, for at least two reasons.First, it is true that studies that terminate early at the H1 boundary will, on average, overestimate the true effect. This conditional bias, however, is balanced by late terminations, which will, on average, underestimate the true effect. Early terminations have a smaller sample size than late terminations, and consequently receive less weight in a meta-analysis. When all studies (i.e., early and late terminations) are considered together, the bias is negligible (Berry, Bradley, & Connor, 2010; Fan, DeMets, & Lan, 2004; Goodman, 2007; Schönbrodt et al., 2015). Hence, the sequential procedure is approximately unbiased overall.Second, the conditional bias of early terminations is conceptually equivalent to the bias that results when only significant studies are reported and non-significant studies disappear into the file drawer (Goodman, 2007). In all experimental designs –whether sequential, non-sequential, frequentist, or Bayesian– the average effect size inevitably increases when one selectively averages studies that show a larger-than-average effect size. Selective publishing is a concern across the board, and an unbiased research synthesis requires that one considers significant and non-significant results, as well as early and late terminations.Although sequential designs have negligible unconditional bias, it may nevertheless be desirable to provide a principled “correction” for the conditional bias at early terminations, in particular when the effect size of a single study is evaluated. For this purpose, Goodman (2007) outlines a Bayesian approach that uses prior expectations about plausible effect sizes. This approach shrinks extreme estimates from early terminations towards more plausible regions. Smaller sample sizes are naturally more sensitive to prior-induced shrinkage, and hence the proposed correction fits the fact that most extreme deviations from the true value are found in very early terminations that have a small sample size (Schönbrodt et al., 2015).

library(dplyr)

library(htmlTable)

# set seed for reproducibility

set.seed(0xBEEF)

trueLevel <- 3

trueSD <- 2

safeLevel <- 2.7

maxN <- 50

minN <- 3

B <- 10000 # number of Monte Carlo simulations

res <- data.frame()

for (i in 1:B) {

print(paste0(i, "/", B))

maxSample <- rnorm(maxN, trueLevel, trueSD)

# optional stopping

for (n in minN:maxN) {

t0 <- t.test(maxSample[1:n], mu=safeLevel, alternative="less")

#print(paste0("n=", n, "; ", t0$estimate, ": ", t0$p.value))

if (t0$p.value <= .05) break;

}

finalSample.seq <- maxSample[1:n]

# now construct a matched fixed-n

finalSample.fixed <- rnorm(n, trueLevel, trueSD)

# ---------------------------------------------------------------------

# save results in long format

# sequential design

res <- rbind(res, data.frame(

id = i,

type = "sequential",

n = n,

p.value = t0$p.value,

selected = t0$p.value <= .05,

empMean = mean(finalSample.seq)

))

# fixed design

res <- rbind(res, data.frame(

id = i,

type = "fixed",

n = n,

p.value = NA,

selected = mean(finalSample.fixed) <= safeLevel, # some arbitrary publication bias selection

empMean = mean(finalSample.fixed)

))

}

save(res, file="res.RData")

# load("res.RData")

# Figure 1: Sampling distribution

ggplot(res, aes(x=n, y=empMean)) + geom_jitter(height=0, alpha=0.15) + xlab("Sample size") + ylab("Sample mean") + geom_hline(yintercept=trueLevel, color="red") + facet_wrap(~type) + theme_bw()

# Figure 2: Individual study estimates

ggplot(res, aes(x=empMean)) + geom_density() + xlab("Sample mean") + geom_vline(xintercept=trueLevel, color="red") + facet_wrap(~type) + theme_bw()

# the mean estimate of all late terminations

res %>% group_by(type) %>% filter(n==50) %>% summarise(lateEst = mean(empMean))

# how many strategy A studies were significant?

res %>% filter(type=="sequential") %>% .[["selected"]] %>% table()

# Compute estimated lead levels

est.noBias <- res %>% group_by(type) %>% dplyr::summarise(

bias = FALSE,

naive.mean = mean(empMean),

weighted.mean = weighted.mean(empMean, w=n)

)

est.Bias <- res %>% filter(selected==TRUE) %>% group_by(type) %>% dplyr::summarise(

bias = TRUE,

naive.mean = mean(empMean),

weighted.mean = weighted.mean(empMean, w=n)

)

est <- rbind(est.noBias, est.Bias)

est

# output a html table

est.display <- txtRound(data.frame(est), 2, excl.cols=1:2)

t1 <- htmlTable(est.display,

header = c("Sampling plan", "PubBias", "Naive mean", "Weighted mean"),

rnames = FALSE)

t1

cat(t1)

# LMU psychology department distributes funding based on criteria of research transparency

**change the incentive structure towards reproducible and open science**. The internal distribution of funding now partly is based on transparency criteria: Publications with open data, open material and pre-registrations get bonus points which directly translate into larger money allocations for that research unit.

# Changing hiring practices towards research transparency: The first open science statement in a professorship advertisement

Engaging in open science practices increases knowledge as a common good, and ensures the reproducibility, verifiability and credibility of research. But some have the fear that on an individual strategic level (in particular from an early career perspective) engaging in research transparency could reduce a researcher’s chance to get a tenured position in academia.

University hiring decisions often are driven (amongst other criteria) by publication quantity and journal prestige: “Several universities base promotion decisions on threshold *h*-index values and on the number of articles in ‘high-impact’ journals” (Hicks, Wouters, Waltman, de Rijcke, & Rafols, 2015), and Nosek, Spies, & Motyl (2012) mention “[…] the prevailing perception that publication numbers and journal prestige are the key drivers for professional success”.

We all know where this focus on pure quantity and too-perfect results led us: “In a world where researchers are rewarded for how many papers they publish, this can lead to a decrease in the truth value of our shared knowledge” (Nelson, Simmons, & Simonsohn, 2012), which can be seen in ongoing debates about low replication rates in psychology, medicine, or economics.

Doing studies with high statistical power, preparing open data, and trying to publish realistic results that are not hacked to (unrealistic) perfection will slow down scientists. Researchers engaging in these good research practices probably will have a smaller quantity of publications, and if that is the major selection criterion, they have a disadvantage in a competitive job market for tenured positions.

**For this reason, hiring standards have to change as well towards a valuation of research transparency, and the department of psychology at LMU München did the first step into this direction.**

Based on a suggestion of our Open Science Committee, the department added a paragraph to a professorship job advertisement which asks for an open science statement from the candidates:

Here’s a translation of the open science paragraph:

Our department embraces the values of open science and strives for replicable and reproducible research. For this goal we support transparent research with open data, open material, and pre-registrations. Candidates are asked to describe in what way they already pursued and plan to pursue these goals.

This paragraph clearly communicates open science as a core value of our department.

Of course, criteria of research transparency will not be the only criteria of evaluation for candidates. But, to my knowledge, this is the first time that they are *explicit* criteria.

Jean-Claude Burgelman (Directorate General for Research and Innovation of the European Commission) says that “the career system has to gratify open science”. I hope that many more universities will follow the LMU’s lead with an explicit commitment to open science in their hiring practices.