Tukey on Decisions and Conclusions

In 1955 Tukey gave a dinner talk about the difference between decisions and conclusions at a meeting of the Section of Physical and Engineering Science of the American Statistical Association. The talk was published in 1960. The distinction relates directly to different goals researchers might have when they collect data. This blog is largely a summary of his paper.

 

Tukey was concerned about the ‘tendency of decision theory to attempt to conquest all of statistics’. In hindsight, he needn’t have worried. In the social sciences, most statistics textbooks do not even discuss decision theory. His goal was to distinguish decisions from conclusions, to carve out a space for ‘conclusion theory’ to complement decision theory. He distinguishes decisions from conclusions.

 

In practice, making a decision means to ‘decide to act for the present as if’. Possible actions are defined, possible states of nature identified, and we make an inference about each state of nature. Decisions can be made even when we remain extremely uncertain about any ‘truth’. Indeed, in extreme cases we can even make decisions without access to any data. We might even decide to act as if two mutually exclusive states of nature are true! For example, we might buy a train ticket for a holiday three months from now, but also take out life insurance in case we die tomorrow.   

 

Conclusions differ from decisions. First, conclusions are established without taking consequences into consideration. Second, conclusions are used to build up a ‘fairly well-established body of knowledge’. As Tukey writes: “A conclusion is a statement which is to be accepted as applicable to the conditions of an experiment or observation unless and until unusually strong evidence to the contrary arises.” A conclusion is not a decision on how to act in the present. Conclusions are to be accepted, and thereby incorporated into what Frick (1996) calls a ‘corpus of findings’. According to Tukey, conclusions are used to narrow down the number of working hypotheses still considered consistent with observations. Conclusions should be reached, not based on their consequences, but because of their lasting (but not everlasting, as conclusions can now and then be overturned by new evidence) contribution to scientific knowledge.

 

Tests of hypotheses

 

According to Tukey, a test of hypotheses can have two functions. The first function is as a decision procedure, and the second function is to reach a conclusion. In a decision procedure the goal is to choose a course of action given an acceptable risk. This risk can be high. For example, a researcher might decide not to pursue a research idea after a first study, designed to have 80% power for a smallest effect size of interest, yields a non-significant result. The error rate is at most 20%, but the researcher might have enough good research ideas to not care.

 

The second function is to reach a conclusion. This is done, according to Tukey, by controlling the Type 1 and Type 2 error rate at ‘suitably low levels’ (Note: Tukey’s discussion of concluding an effect is absent is hindered somewhat by the fact that equivalence tests were not yet widely established in 1955 – Hodges & Lehman’s paper appeared in 1954). Low error rates, such as the conventions to use a 5% of 1% alpha level, are needed to draw conclusions that can enter the corpus of findings (even though some of these conclusions will turn out to be wrong, in the long run).

 

Why would we need conclusions?

 

One might reasonably wonder if we need conclusions in science. Tukey also ponders this question in Appendix 2. He writes “Science, in the broadest sense, is both one of the most successful of human affairs, and one of the most decentralized. In principle, each of us puts his evidence (his observations, experimental or not, and their discussion) before all the others, and in due course an adequate consensus of opinion develops.” He argues not for an epistemological reason, nor for a statistical reason, but for a sociological reason. Tukey writes: “There are four types of difficulty, then, ranging from communication through assessment to mathematical treatment, each of which by itself will be sufficient, for a long time, to prevent the replacement, in science, of the system of conclusions by a system based more closely on today’s decision theory.” He notes how scientists can no longer get together in a single room (as was somewhat possible in the early decades of the Royal Society of London) to reach consensus about decisions. Therefore, they need to communicate conclusions, as “In order to replace conclusions as the basic means of communication, it would be necessary to rearrange and replan the entire fabric of science.” 

 

I hadn’t read Tukey’s paper when we wrote our preprint “The Epistemic and Pragmatic Function of Dichotomous Claims Based on Statistical Hypothesis Tests”. In this preprint, we also discuss a sociological reason for the presence of dichotomous claims in science. We also ask: “Would it be possible to organize science in a way that relies less on tests of competing theories to arrive at intersubjectively established facts about phenomena?” and similarly conclude: “Such alternative approaches seem feasible if stakeholders agree on the research questions that need to be investigated, and methods to be utilized, and coordinate their research efforts”.  We should add a citation to Tukey's 1960 paper.

 

Is the goal of an study a conclusion, a decision, or both?

 

Tukey writes he “looks forward to the day when the history and status of tests of hypotheses will have been disentangled.” I think that in 2022 that day has not yet come. At the same time, Tukey admits in Appendix 1 that the two are sometimes intertwined.

 

A situation Tukey does not discuss, but that I think is especially difficult to disentangle, is a cumulative line of research. Although I would prefer to only build on an established corpus of findings, this is simply not possible. Not all conclusions in the current literature are reached with low error rates. This is true both for claims about the absence of an effect (which are rarely based on an equivalence test against a smallest effect size of interest with a low error rate), as for claims about the presence of an effect, not just because of p-hacking, but also because I might want to build on an exploratory finding from a previous study. In such cases, I would like to be able to conclude the effects I build on are established findings, but more often than not, I have to decide these effects are worth building on. The same holds for choices about the design of a set of studies in a research line. I might decide to include a factor in a subsequent study, or drop it. These decisions are based on conclusions with low error rates if I had the resources to collect large samples and perform replication studies, but other times they involve decisions about how to act in my next study with quite considerable risk.

 

We allow researchers to publish feasibility studies, pilot studies, and exploratory studies. We don’t require every study to be a Registered Report of Phase 3 trial. Not all information in the literature that we build on has been established with the rigor Tukey associates with conclusions. And the replication crisis has taught us that more conclusions from the past are later rejected than we might have thought based on the alpha levels reported in the original articles. And in some research areas, where data is scarce, we might need to accept that, if we want to learn anything, the conclusions will always more tentative (and the error rates accepted in individual studies will be higher) than in research areas where data is abundant.

 

Even if decisions and conclusions can not be completely disentangled, reflecting on their relative differences is very useful, as I think it can help us to clarify the goal we have when we collect data. 

 

For a 2013 blog post by Justin Esarey, who found the distinction a bit less useful than I found it, see https://polmeth.org/blog/scientific-conclusions-versus-scientific-decisions-or-we%E2%80%99re-having-tukey-thanksgiving

 

References

Frick, R. W. (1996). The appropriate use of null hypothesis testing. Psychological Methods, 1(4), 379–390. https://doi.org/10.1037/1082-989X.1.4.379

Tukey, J. W. (1960). Conclusions vs decisions. Technometrics, 2(4), 423–433.

Uygun Tunç, D., Tunç, M. N., & Lakens, D. (2021). The Epistemic and Pragmatic Function of Dichotomous Claims Based on Statistical Hypothesis Tests. PsyArXiv. https://doi.org/10.31234/osf.io/af9by

 

 

 

 

 

Not All Flexibility P-Hacking Is, Young Padawan

During a recent workshop on Sample Size Justification an early career researcher asked me: “You recommend sequential analysis in your paper for when effect sizes are uncertain, where researchers collect data, analyze the data, stop when a test is significant, or continue data collection when a test is not significant, and, I don’t want to be rude, but isn’t this p-hacking?”

In linguistics there is a term for when children apply a rule they have learned to instances where it does not apply: Overregularization. They learn ‘one cow, two cows’, and use the +s rule for plural where it is not appropriate, such as ‘one mouse, two mouses’ (instead of ‘two mice’). The early career researcher who asked me if sequential analysis was a form of p-hacking was also overregularizing. We teach young researchers that flexibly analyzing data inflates error rates, is called p-hacking, and is a very bad thing that was one of the causes of the replication crisis. So, they apply the rule ‘flexibility in the data analysis is a bad thing’ to cases where it does not apply, such as in the case of sequential analyses. Yes, sequential analyses give a lot of flexibility to stop data collection, but it does so while carefully controlling error rates, with the added bonus that it can increase the efficiency of data collection. This makes it a good thing, not p-hacking.

 

Children increasingly use correct language the longer they are immersed in it. Many researchers are not yet immersed in an academic environment where they see flexibility in the data analysis applied correctly. Many are scared to do things wrong, which risks becoming overly conservative, as the pendulum from ‘we are all p-hacking without realizing the consequences’ swings back to far to ‘all flexibility is p-hacking’. Therefore, I patiently explain during workshops that flexibility is not bad per se, but that making claims without controlling your error rate is problematic.

In a recent podcast episode of ‘Quantitude’ one of the hosts shared a similar experience 5 minutes into the episode. A young student remarked that flexibility during the data analysis was ‘unethical’. The remainder of the podcast episode on ‘researcher degrees of freedom’ discussed how flexibility is part of data analysis. They clearly state that p-hacking is problematic, and opportunistic motivations to perform analyses that give you what you want to find should be constrained. But they then criticized preregistration in ways many people on Twitter disagreed with. They talk about ‘high priests’ who want to ‘stop bad people from doing bad things’ which they find uncomfortable, and say ‘you can not preregister every contingency’. They remark they would be surprised if data could be analyzed without requiring any on the fly judgment.

Although the examples they gave were not very good¹ it is of course true that researchers sometimes need to deviate from an analysis plan. Deviating from an analysis plan is not p-hacking. But when people talk about preregistration, we often see overregularization: “Preregistration requires specifying your analysis plan to prevent inflation of the Type 1 error rate, so deviating from a preregistration is not allowed.” The whole point of preregistration is to transparently allow other researchers to evaluate the severity of a test, both when you stick to the preregistered statistical analysis plan, as when you deviate from it. Some researchers have sufficient experience with the research they do that they can preregister an analysis that does not require any deviations², and then readers can see that the Type 1 error rate for the study is at the level specified before data collection. Other researchers will need to deviate from their analysis plan because they encounter unexpected data. Some deviations reduce the severity of the test by inflating the Type 1 error rate. But other deviations actually get you closer to the truth. We can not know which is which. A reader needs to form their own judgment about this.

A final example of overregularization comes from a person who discussed a new study that they were preregistering with a junior colleague. They mentioned the possibility of including a covariate in an analysis but thought that was too exploratory to be included in the preregistration. The junior colleague remarked: “But now that we have thought about the analysis, we need to preregister it”. Again, we see an example of overregularization. If you want to control the Type 1 error rate in a test, preregister it, and follow the preregistered statistical analysis plan. But researchers can, and should, explore data to generate hypotheses about things that are going on in their data. You can preregister these, but you do not have to. Not exploring data could even be seen as research waste, as you are missing out on the opportunity to generate hypotheses that are informed by data. A case can be made that researchers should regularly include variables to explore (e.g., measures that are of general interest to peers in their field), as long as these do not interfere with the primary hypothesis test (and as long as these explorations are presented as such).

In the book “Reporting quantitative research in psychology: How to meet APA Style Journal Article Reporting Standards” by Cooper and colleagues from 2020 a very useful distinction is made between primary hypotheses, secondary hypotheses, and exploratory hypotheses. The first consist of the main tests you are designing the study for. The secondary hypotheses are also of interest when you design the study – but you might not have sufficient power to detect them. You did not design the study to test these hypotheses, and because the power for these tests might be low, you did not control the Type 2 error rate for secondary hypotheses. You can preregister secondary hypotheses to control the Type 1 error rate, as you know you will perform them, and if there are multiple secondary hypotheses, as Cooper et al (2020) remark, readers will expect “adjusted levels of statistical significance, or conservative post hoc means tests, when you conducted your secondary analysis”.

If you think of the possibility to analyze a covariate, but decide this is an exploratory analysis, you can decide to neither control the Type 1 error rate nor the Type 2 error rate. These are analyses, but not tests of a hypothesis, as any findings from these analyses have an unknown Type 1 error rate. Of course, that does not mean these analyses can not be correct in what they reveal – we just have no way to know the long run probability that exploratory conclusions are wrong. Future tests of the hypotheses generated in exploratory analyses are needed. But as long as you follow Journal Article Reporting Standards and distinguish exploratory analyses, readers know what the are getting. Exploring is not p-hacking.

People in psychology are re-learning the basic rules of hypothesis testing in the wake of the replication crisis. But because they are not yet immersed in good research practices, the lack of experience means they are overregularizing simplistic rules to situations where they do not apply. Not all flexibility is p-hacking, preregistered studies do not prevent you from deviating from your analysis plan, and you do not need to preregister every possible test that you think of. A good cure for overregularization is reasoning from basic principles. Do not follow simple rules (or what you see in published articles) but make decisions based on an understanding of how to achieve your inferential goal. If the goal is to make claims with controlled error rates, prevent Type 1 error inflation, for example by correcting the alpha level where needed. If your goal is to explore data, feel free to do so, but know these explorations should be reported as such. When you design a study, follow the Journal Article Reporting Standards and distinguish tests with different inferential goals.

 

¹ E.g., they discuss having to choose between Student’s t-test and Welch’s t-test, depending on wheter Levene’s test indicates the assumption of homogeneity is violated, which is not best practice – just follow R, and use Welch’s t-test by default.

² But this is rare – only 2 out of 27 preregistered studies in Psychological Science made no deviations. https://royalsocietypublishing.org/doi/full/10.1098/rsos.211037 We can probably do a bit better if we only preregistered predictions at a time where we really understand our manipulations and measures.

The Red Team Challenge (Part 3): Is it Feasible in Practice?

By Daniel Lakens & Leo Tiokhin

Also read Part 1 and Part 2 in this series on our Red Team Challenge.

Six weeks ago, we launched the Red Team Challenge: a feasibility study to see whether it could be worthwhile to pay people to find errors in scientific research. In our project, we wanted to see to what extent a “Red Team” - people hired to criticize a scientific study with the goal to improve it - would improve the quality of the resulting scientific work.

Currently, the way that error detection works in science is a bit peculiar. Papers go through the peer-review process and get the peer-reviewed “stamp of approval”. Then, upon publication, some of these same papers receive immediate and widespread criticism. Sometimes this even leads to formal corrections or retractions. And this happens even at some of the most prestigious scientific journals.

So, it seems that our current mechanisms of scientific quality control leave something to be desired. Nicholas Coles, Ruben Arslan, and the authors of this post (Leo Tiokhin and Daniël Lakens) were interested in whether Red Teams might be one way to improve quality control in science.

Ideally, a Red Team joins a research project from the start and criticizes each step of the process. However, doing this would have taken the duration of an entire study. At the time, it also seemed a bit premature -- we didn’t know whether anyone would be interested in a Red Team approach, how it would work in practice, and so on. So, instead, Nicholas Coles, Brooke Frohlich, Jeff Larsen, and Lowell Gaertner volunteered one of their manuscripts (a completed study that they were ready to submit for publication). We put out a call on Twitter, Facebook, and the 20% Statistician blog, and 22 people expressed interest. On May 15^th, we randomly selected five volunteers based on five areas of expertise: Åse Innes-Ker (affective science), Nicholas James (design/methods), Ingrid Aulike (statistics), Melissa Kline (computational reproducibility), and Tiago Lubiana (wildcard category). The Red Team was then given three weeks to report errors.

Our Red Team project was somewhat similar to traditional peer review, except that we 1) compensated Red Team members’ time with a $200 stipend, 2) explicitly asked the Red Teamers to identify errors in any part of the project (i.e., not just writing), 3) gave the Red Team full access to the materials, data, and code, and 4) provided financial incentives for identifying critical errors (a donation to the GiveWell charity non-profit for each unique “critical error” discovered).

The Red Team submitted 107 error reports. Ruben Arslan--who helped inspire this project with his Bug Bounty Program--served as the neutral arbiter. Ruben examined the reports, evaluated the authors’ responses, and ultimately decided whether an issue was “critical” (see this post for Ruben’s reflection on the Red Team Challenge) Of the 107 reports, Ruben concluded that there were 18 unique critical issues (for details, see this project page). Ruben decided that any major issues that potentially invalidated inferences were worth $100, minor issues related to computational reproducibility were worth $20, and minor issues that could be resolved without much work were worth $10. After three weeks, the total final donation was $660. The Red Team detected 5 major errors. These included two previously unknown limitations of a key manipulation, inadequacies in the design and description of the power analysis, an incorrectly reported statistical test in the supplemental materials, and a lack of information about the sample in the manuscript. Minor issues concerned reproducibility of code and clarifications about the procedure.

After receiving this feedback, Nicholas Coles and his co-authors decided to hold off submitting their manuscript (see this post for Nicholas’ personal reflection). They are currently conducting a new study to address some of the issues raised by the Red Team.

We consider this to be a feasibility study of whether a Red Team approach is practical and worthwhile. So, based on this study, we shouldn’t draw any conclusions about a Red Team approach in science except one: it can be done.

That said, our study does provide some food for thought. Many people were eager to join the Red Team. The study’s corresponding author, Nicholas Coles, was graciously willing to acknowledge issues when they were pointed out. And it was obvious that, had these issues been pointed out earlier, the study would have been substantially improved before being carried out. These findings make us optimistic that Red Teams can be useful and feasible to implement.

In an earlier column, the issue was raised that rewarding Red Team members with co-authorship on the subsequent paper would create a conflict of interest -- too severe criticism on the paper might make the paper unpublishable. So, instead, we paid each Red Teamer $200 for their service. We wanted to reward people for their time. We did not want to reward them only for finding issues because, before we knew that 19 unique issues would be found, we were naively worried that the Red Team might find few things wrong with the paper. In interviews with Red Team members, it became clear that the charitable donations for each issue were not a strong motivator. Instead, people were just happy to detect issues for decent pay. They didn't think that they deserved authorship for their work, and several Red Team members didn't consider authorship on an academic paper to be valuable, given their career goals.

After talking with the Red Team members, we started to think that certain people might enjoy Red Teaming as a job – it is challenging, requires skills, and improves science. This opens up the possibility of a freelance services marketplace (such as Fiverr) for error detection, where Red Team members are hired at an hourly rate and potentially rewarded for finding errors. It should be feasible to hire people to check for errors at each phase of a project, depending on their expertise and reputation as good error-detectors. If researchers do not have money for such a service, they might be able to set up a volunteer network where people “Red Team” each other’s projects. It could also be possible for universities to create Red Teams (e.g., Cornell University has a computational reproducibility service that researchers can hire).

As scientists, we should ask ourselves when, and for which type of studies, we want to invest time and/or money to make sure that published work is as free from errors as possible. As we continue to consider ways to increase the reliability of science, a Red Team approach might be something to further explore.

What’s a family in family-wise error control?

When you perform multiple comparisons in a study, you need to control your alpha level for multiple comparisons. It is generally recommended to control for the family-wise error rate, but there is some confusion about what a 'family' is. As Bretz, Hothorn, & Westfall (2011) write in their excellent book “Multiple Comparisons Using R” on page 15: “The appropriate choice of null hypotheses being of primary interest is a controversial question. That is, it is not always clear which set of hypotheses should constitute the family H₁,…,H_m. This topic has often been in dispute and there is no general consensus.” In one of the best papers on controlling for multiple comparisons out there, Bender & Lange (2001) write: “Unfortunately, there is no simple and unique answer to when it is appropriate to control which error rate. Different persons may have different but nevertheless reasonable opinions. In addition to the problem of deciding which error rate should be under control, it has to be defined first which tests of a study belong to one experiment.” The Wikipedia page on family-wise error rate is a mess.

I will be honest: I have never understood this confusion about what a family of tests is when controlling the family-wise error rate. At least not in a Neyman-Pearson approach to hypothesis testing, where the goal is to use data to make decisions about how to act. Neyman (Neyman, 1957) calls his approach inductive behavior. The outcome of an experiment leads one to take different possible actions, which can be either practical (e.g., implement a new procedure, abandon a research line) or scientific (e.g., claim there is or is no effect). From an error-statistical approach (Mayo, 2018) inflated Type 1 error rates mean that it has become very likely that you will be able to claim support for your hypothesis, even when the hypothesis is wrong. This reduces the severity of the test. To prevent this, we need to control our error rate at the level of our claim.

One reason the issue of family-wise error rates might remain vague, is that researchers are often vague about their claims. We do not specify our hypotheses unambiguously, and therefore this issue remains unclear. To be honest, I suspect another reason there is a continuing debate about whether and how to lower the alpha level to control for multiple comparisons in some disciplines is that 1) there are a surprisingly large number of papers written on this topic that argue you do not need to control for multiple comparisons, which are 2) cited a huge number of times giving rise to the feeling that surely they must have a point. Regrettably, the main reason these papers are written is because there are people who don't think a Neyman-Pearson approach to hypothesis testing is a good idea, and the main reason these papers are cited is because doing so is convenient for researchers who want to publish statistically significant results, as they can justify why they are not lowering their alpha level, making that p = 0.02 in one of three tests really 'significant'. All papers that argue against the need to control for multiple comparisons when testing hypotheses are wrong.  Yes, their existence and massive citation counts frustrate me. It is fine not to test a hypothesis, but when you do, and you make a claim based on a test, you need to control your error rates. 

But let’s get back to our first problem, which we can solve by making the claims people need to control Type 1 error rates for less vague. Lisa DeBruine and I recently proposed machine readable hypothesis tests to remove any ambiguity in the tests we will perform to examine statistical predictions, and when we will consider a claim corroborated or falsified. In this post, I am going to use our R package ‘scienceverse’ to clarify what constitutes a family of tests when controlling the family-wise error rate.

An example of formalizing family-wise error control

Let’s assume we collect data from 100 participants in a control and treatment condition. We collect 3 dependent variables (dv1, dv2, and dv3). In the population there is no difference between groups on any of these three variables (the true effect size is 0). We will analyze the three dv’s in independent t-tests. This requires specifying our alpha level, and thus deciding whether we need to correct for multiple comparisons. How we control error rates depends on claim we want to make.

We might want to act as if (or claim that) our treatment works if there is a difference between the treatment and control conditions on any of the three variables. In scienceverse terms, this means we consider the prediction corroborated when the p-value of the first t-test is smaller than alpha level, the p-value of the second t-test is smaller than the alpha level, or the p-value of the first t-test is smaller than the alpha level. In the scienceverse code, we specify a criterion for each test (a p-value smaller than the alpha level, p.value < alpha_level) and conclude the hypothesis is corroborated if either of these criteria are met ("p_t_1 | p_t_2 | p_t_3").  

We could also want to make three different predictions. Instead of one hypothesis (“something will happen”) we have three different hypotheses, and predict there will be an effect on dv1, dv2, and dv3. The criterion for each t-test is the same, but we now have three hypotheses to evaluate (H1, H2, and H3). Each of these claims can be corroborated, or not.

Scienceverse allows you to specify your hypotheses tests unambiguously (for code used in this blog, see the bottom of the post). It also allows you to simulate a dataset, which we can use to examine Type 1 errors by simulating data where no true effects exist. Finally, scienceverse allows you to run the pre-specified analyses on the (simulated) data, and will automatically create a report that summarizes which hypotheses were corroborated (which is useful when checking if the conclusions in a manuscript indeed follow from the preregistered analyses, or not). The output a single simulated dataset for the scenario where we will interpret any effect on the three dv’s as support for the hypothesis looks like this:

Evaluation of Statistical Hypotheses

12 March, 2020

Simulating Null Effects Postregistration

Results

Hypothesis 1: H1

Something will happen

• p_t_1 is confirmed if analysis ttest_1 yields p.value<0.05
  
  The result was p.value = 0.452 (FALSE)
  
  
• p_t_2 is confirmed if analysis ttest_2 yields p.value<0.05
  
  The result was p.value = 0.21 (FALSE)
  
  
• p_t_3 is confirmed if analysis ttest_3 yields p.value<0.05
  
  The result was p.value = 0.02 (TRUE)

Corroboration ( TRUE )

The hypothesis is corroborated if anything is significant.

 p_t_1 | p_t_2 | p_t_3 

Falsification ( FALSE )

The hypothesis is falsified if nothing is significant.

 !p_t_1 & !p_t_2 & !p_t_3 

All criteria were met for corroboration.

We see the hypothesis that ‘something will happen’ is corroborated, because there was a significant difference on dv3 - even though this was a Type 1 error, since we simulated data with a true effect size of 0 - and any difference was taken as support for the prediction. With a 5% alpha level, we will observe 1-(1-0.05)^3 = 14.26% Type 1 errors in the long run. This Type 1 error inflation can be prevented by lowering the alpha level, for example by a Bonferroni correction (0.05/3), after which the expected Type 1 error rate is 4.92% (see Bretz et al., 2011, for more advanced techniques to control error rates). When we examine the report for the second scenario, where each dv tests a unique hypothesis, we get the following output from scienceverse:

Evaluation of Statistical Hypotheses

12 March, 2020

Simulating Null Effects Postregistration

Results

Hypothesis 1: H1

dv1 will show an effect

• p_t_1 is confirmed if analysis ttest_1 yields p.value<0.05
  
  The result was p.value = 0.452 (FALSE)

Corroboration ( FALSE )

The hypothesis is corroborated if dv1 is significant.

 p_t_1 

Falsification ( TRUE )

The hypothesis is falsified if dv1 is not significant.

 !p_t_1 

All criteria were met for falsification.

Hypothesis 2: H2

dv2 will show an effect

• p_t_2 is confirmed if analysis ttest_2 yields p.value<0.05
  
  The result was p.value = 0.21 (FALSE)

Corroboration ( FALSE )

The hypothesis is corroborated if dv2 is significant.

 p_t_2 

Falsification ( TRUE )

The hypothesis is falsified if dv2 is not significant.

 !p_t_2 

All criteria were met for falsification.

Hypothesis 3: H3

dv3 will show an effect

• p_t_3 is confirmed if analysis ttest_3 yields p.value<0.05
  
  The result was p.value = 0.02 (TRUE)

Corroboration ( TRUE )

The hypothesis is corroborated if dv3 is significant.

 p_t_3 

Falsification ( FALSE )

The hypothesis is falsified if dv3 is not significant.

 !p_t_3 

All criteria were met for corroboration.

We now see that two hypotheses were falsified (yes, yes, I know you should not use p > 0.05 to falsify a prediction in real life, and this part of the example is formally wrong so I don't also have to explain equivalence testing to readers not familiar with it - if that is you, read this, and know scienceverse will allow you to specify equivalence test as the criterion to falsify a prediction, see the example here). The third hypothesis is corroborated, even though, as above, this is a Type 1 error.

It might seem that the second approach, specifying each dv as it’s own hypothesis, is the way to go if you do not want to lower the alpha level to control for multiple comparisons. But take a look at the report of the study you have performed. You have made 3 predictions, of which 1 was corroborated. That is not an impressive success rate. Sure, mixed results happen, and you should interpret results not just based on the p-value (but on the strength of the experimental design, assumptions about power, your prior, the strength of the theory, etc.) but if these predictions were derived from the same theory, this set of results is not particularly impressive. Since researchers can never selectively report only those results that ‘work’ because this would be a violation of the code of research integrity, we should always be able to see the meager track record of predictions.If you don't feel ready to make a specific predictions (and run the risk of sullying your track record) either do unplanned exploratory tests, and do not make claims based on their results, or preregister all possible tests you can think of, and massively lower your alpha level to control error rates (for example, genome-wide association studies sometimes use an alpha level of 5 x 10–8 to control the Type 1 erorr rate).

Hopefully, specifying our hypotheses (and what would corroborate them) transparently by using scienceverse makes it clear what happens in the long run in both scenarios. In the long run, both the first scenario, if we would use an alpha level of 0.05/3 instead of 0.05, and the second scenario, with an alpha level of 0.05 for each individual hypothesis, will lead to the same end result: Not more than 5% of our claims will be wrong, if the null hypothesis is true. In the first scenario, we are making one claim in an experiment, and in the second we make three. In the second scenario we will end up with more false claims in an absolute sense, but the relative number of false claims is the same in both scenarios. And that’s exactly the goal of family-wise error control.

References

Bender, R., & Lange, S. (2001). Adjusting for multiple testing—When and how? Journal of Clinical Epidemiology, 54(4), 343–349.

Bretz, F., Hothorn, T., & Westfall, P. H. (2011). Multiple comparisons using R. CRC Press.

Mayo, D. G. (2018). Statistical inference as severe testing: How to get beyond the statistics wars. Cambridge University Press.

Neyman, J. (1957). “Inductive Behavior” as a Basic Concept of Philosophy of Science. Revue de l’Institut International de Statistique / Review of the International Statistical Institute, 25(1/3), 7. https://doi.org/10.2307/1401671

Thanks to Lisa DeBruine for feedback on an earlier draft of this blog post.

Observed Type 1 Error Rates (Why Statistical Models are Not Reality)

“In the long run we are all dead.” - John Maynard Keynes

When we perform hypothesis tests in a Neyman-Pearson framework we want to make decisions while controlling the rate at which we make errors. We do this in part by setting an alpha level that guarantees we will not say there is an effect when there is no effect more than α% of the time, in the long run.

I like my statistics applied. And in practice I don’t do an infinite number of studies. As Keynes astutely observed, I will be dead before then. So when I control the error rate for my studies, what is a realistic Type 1 error rate I will observe in the ‘somewhat longer run’?

Let’s assume you publish a paper that contains only a single p-value. Let’s also assume the true effect size is 0, so the null hypothesis is true. Your test will return a p-value smaller than your alpha level (and this would be a Type 1 error) or not. With a single study, you don’t have the granularity to talk about a 5% error rate.

In experimental psychology 30 seems to be a reasonable average for the number of p-values that are reported in a single paper (http://doi.org/10.1371/journal.pone.0127872). Let’s assume you perform 30 tests in a single paper and every time the null is true (even though this is often unlikely in a real paper). In the long run, with an alpha level of 0.05 we can expect that 30 * 0.05 = 1.5 p-values will be significant. But in real sets of 30 p-values there is no half of a p-value, so you will either observe 0, 1, 2, 3, 4, 5, or even more Type 1 errors, which equals 0%, 3.33%, 6.66%, 10%, 13.33%, 16.66%, or even more. We can plot the frequency of Type 1 error rates for 1 million sets of 30 tests.

Each of these error rates occurs with a certain frequency. 21.5% of the time, you will not make any Type 1 errors. 12.7% of the time, you will make 3 Type 1 errors in 30 tests. The average over thousands of papers reporting 30 tests will be a Type 1 error rate of 5%, but no single set of studies is average.

Now maybe a single paper with 30 tests is not ‘long runnerish’ enough. What we really want to control the Type 1 error rate of is the literature, past, present, and future. Except, we will never read the literature. So let’s assume we are interested in a meta-analysis worth of 200 studies that examine a topic where the true effect size is 0 for each test. We can plot the frequency of Type 1 error rates for 1 million sets of 200 tests.
 

Now things start to look a bit more like what you would expect. The Type 1 error rate you will observe in your set of 200 tests is close to 5%. However, it is almost exactly as likely that the observed Type 1 error rate is 4.5%. 90% of the distribution of observed alpha levels will lie between 0.025 and 0.075. So, even in ‘somewhat longrunnish’ 200 tests, the observed Type 1 error rate will rarely be exactly 5%, and it might be more useful to think about it as being between 2.5 and 7.5%.

Statistical models are not reality.

A 5% error rate exists only in the abstract world of infinite repetitions, and you will not live long enough to perform an infinite number of studies. In practice, if you (or a group of researchers examining a specific question) do real research, the error rates are somewhere in the range of 5%. Everything has variation in samples drawn from a larger population - error rates are no exception.

When we quantify things, there is the tendency to get lost in digits. But in practice, the levels of random noise we can reasonable expect quickly overwhelms everything at least 3 digits after the decimal. I know we can compute the alpha level after a Pocock correction for two looks at the data in sequential analyses as 0.0294. But this is not the level of granularity that we should have in mind when we think of the error rate we will observe in real lines of research. When we control our error rates, we do so with the goal to end up somewhere reasonably low, after a decent number of hypotheses have been tested. Whether we end up observing 2.5% Type 1 errors or 7.5% errors: Potato, patato.

This does not mean we should stop quantifying numbers precisely when they can be quantified precisely, but we should realize what we get from the statistical procedures we use. We don't get a 5% Type 1 error rate in any real set of studies we will actually perform. Statistical inferences guide us roughly to where we would ideally like to end up. By all means calculate exact numbers where you can. Strictly adhere to hard thresholds to prevent you from fooling yourself too often. But maybe in 2020 we can learn to appreciate statistical inferences are always a bit messy. Do the best you reasonably can, but don’t expect perfection. In 2020, and in statistics.


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For a related paper on alpha levels that in practical situations can not be 5%, see https://psyarxiv.com/erwvk/ by Casper Albers.