The following is a hypothetical exchange between a graduate student and Professor Belfry-Roaster. The names have been changed to protect the innocent….

**Budlie Bond**: Professor Belfry-Roaster I was confused today in journal club when everyone started discussing power. I’ve taken my grad stats courses, but they didn’t teach us anything about power. It seemed really important. But it also seemed controversial. Can you tell me a bit more about power and why people care so much about it

**Prof. Belfry-Roaster**: Sure, power is a very important factor in planning and evaluating research. Technically, power is defined as the long-run probability of rejecting the null hypothesis when it is, in fact, false. Power is typically considered to be a Good Thing because, if the null is false, then you want your research to be capable of rejecting it. The higher the power of your study, the better the chances are that this will happen.

The concept of power comes out of a very specific approach to significance testing pioneered by Neyman and Pearson. In this system, a researcher considers 4 factors when planning and evaluating research: the alpha level (typically the threshold you use to decide whether a finding is statistically significant), the effect size of your focal test of your hypothesis, sample size, and power. The cool thing about this system is that if you know 3 of the factors you can compute the last one. What makes it even easier is that we almost always use an alpha value of .05, so that is fixed. That leaves two things: the effect size (which you don’t control) and your sample size (which you can control). Thus, if you know the effect size of interest, you can use power analysis to determine the sample size needed to reject the null, say, 80% of the time, if the null is false in the population. Similarly, if you know the sample size of a study, you can calculate the power it has to reject the null under a variety of possible effect sizes in the population.

Here’s a classic paper on the topic for some quick reading:

Cohen J. (1992). Statistical power analysis. Current Directions in Psychological Science, 1, 98-101.

**Budlie Bond**: Okay, that is a little clearer. It seems that effect sizes are critical to understanding power. How do I figure out what my effect size is? It seems like that would involve a lot of guess work. I thought part of the reason we did research was because we didn’t know what the effect sizes were.

**Prof. Belfry-Roaster**: Effect sizes refer to the magnitude of the relationship between variables and can be indexed in far too many ways to describe. The two easiest and most useful for the majority of work in our field are the d-score and the correlation coefficient. The d-score is the standardized difference between two means—simply the difference divided by the pooled standard deviation. The correlation coefficient is, well, the correlation coefficient.

The cool thing about these two effect sizes is that they are really easy to compute from the statistics that all papers should report. They can also be derived from basic information in a study, like the sample size and the p-value associated with a focal significance test. So, even if an author has not reported an effect size you can derive one easily from their test statistics. Here are some cool resources that help you understand and calculate effect sizes from basic information like means and standard deviations, p-values, and other test statistics:

https://sites.google.com/site/lakens2/effect-sizes

**Budlie Bond**: You said I can use effect size information to plan a study. How does that work?

**Prof. Belfry-Roaster**: If you have some sense of what the effect size may be based on previous research, you can always use that as a best guess for selecting the appropriate sample size. But, many times that information isn’t available because you are trying something new. If that is the case, you can still draw upon what we generally know about effect sizes in our field. There are now five reviews that show that the average effect sizes in social, personality, and organizational psychology correspond roughly to a d-score of .4 or a correlation of .2.

There are lots of criticisms of these estimates, but they are not a bad starting point for planning purposes. If you plug those numbers into a power calculator, you find that you need about 200 subjects to have 80% power for an average simple main effect (e.g., d = .4). If you want to be safe and either have higher power (e.g., 90%) or plan for a smaller effect size (e.g., d of .3), you’ll need more like 250 to 350 participants. This is pretty close to the sample size when effect sizes get “stable”.

Schoenbrodt & Perugini, 2013; http://www.nicebread.de/at-what-sample-size-do-correlations-stabilize/

However, for other types of analyses, like interaction effects, some smart people have estimated that you’ll need more than twice as many participants—in the range of 500. For example, Uri Simonsohn has shown that if you want to demonstrate that a manipulation can make a previously demonstrated effect go away, you need twice as many participants as you would need to demonstrate the original main effect (http://datacolada.org/17).

Whatever you do, be cautious about these numbers. Your job is to think about these issues not to use rules of thumb blindly. For example, the folks who study genetic effects found out that the effect sizes for single nucleotide polymorphisms were so tiny that they needed hundreds of thousands of people to have enough power to reliably detect their effects. On the flip side, when your effects are big, you don’t need many people. We know that the Stroop effect is both reliable and huge. You only need a handful of people to figure out whether the Stroop main effect will replicate. Your job is to use some estimated effect size to make an informed decision about what your sample size should be. It is not hard to do and there are no good excuses to avoid it.

Here some additional links and tables that you can use to estimate the sample size you will need to reach in order to achieve 80 or 90% power once you’ve got an estimate of your effect size:

For correlations:

https://power.phs.wakehealth.edu/index.cfm?calc=cor

For mean differences:

https://power.phs.wakehealth.edu/index.cfm?calc=tsm

Here’s are two quick and easy tables showing the relation between power and effect size for reference:

**Budlie Bond**: My office-mate Chip Harkel says that there is a new rule of thumb that you should simply get 50 people per cell in an experiment. Is that a sensible strategy to use when I don’t know what the effect size might be?

**Prof. Belfry-Roaster**: The 50 person per cell is better than our previous rules of thumb (e.g., 15 to 20 people per cell), but, with a bit more thought, you can calibrate your sample size better. If you have reasons to think the effect size might be large (like the Stroop Effect), you will waste a lot of resources if you collect 50 cases per cell. Conversely, if you are interested in testing a typical interaction effect, your power is going to be too low using this rule of thumb.

**Budlie Bond**: Why is low power such a bad thing?

**Prof. Belfry-Roaster**: You can think about the answer several ways. Here’s a concrete and personal way to think about it. Let’s say that you are ready to propose your dissertation. You’ve come up with a great idea and we meet to plan out how you are going to test it. Instead of running any subjects I tell you there’s no need. I’m simply going to flip a coin to determine your results. Heads your findings are statistically significant; tails insignificant. Would you agree to that plan? If you find that to be an objectionable plan, then you shouldn’t care for the way we typically design our research because the average power is close to 50% (a coin flip). That’s what you do every time you run a low powered study—you flip a coin. I’d rather that you have a good chance of rejecting the null if it is false then to be subject to the whims of random noise. That’s what having a high powered study can do for you.

At a broader level low power is a problem because the findings from low powered studies are too noisy to rely on. Low powered studies are uninformative. They are also quite possibly the largest reason behind the replication crisis. A lot of people point to p-hacking and fraud as the culprits behind our current crisis, but a much simpler explanation of the problems is that the original studies were so small that they were not capable of revealing anything reliable. Sampling variance is a cruel master. Because of sampling variance, effects in small studies bounce around a lot. If we continue to publish low powered studies, we are contributing to the myth that underpowered studies are capable of producing robust knowledge. They are not.

Here are some additional readings that should help to understand how power is related to increasing the informational value of your research:

Lakens, D., & Evers, E. R. K. (2014). Sailing from the seas of chaos into the corridor of stability: Practical recommendations to increase the informational value of studies. Perspectives on Psychological Science, 9(3), 278–292. http://doi.org/10.1177/1745691614528520

Maxwell, S. E., Kelley, K., & Rausch, J. R. (2008). Sample size planning for statistical power and accuracy in parameter estimation. Annual Review of Psychology, 59(1), 537–563. http://doi.org/10.1146/annurev.psych.59.103006.093735

**Budlie Bond**: Is low power a good reason to dismiss a study after the fact?

**Prof. Belfry-Roaster**. Many people assume that statistical power is not necessary “after the fact.” That is, once we’ve done a study and found a significant result, it would appear that the study must have been capable of detecting said effect. This is based on a misunderstanding of p-values and significance tests (see Fraley & Marks, 2007 for a review).

What many researchers fail to appreciate is that a literature based on underpowered studies is more likely to be full of false positives than a literature that is based on highly powered studies. This sometimes seems counterintuitive to researchers, but it boils down to the fact that, when studies are underpowered, the relative ratio of true to false positives in the literature shifts (see Ioannidis 2008). The consequence is that a literature based on underpowered studies is quite capable of containing an overwhelming number of false positives—much more than the nominal 5% that we’ve been conditioned to expect. If you want to maximize the number of true positives in the literature relative to false leads, you would be wise to not allow underpowered studies into the literature.

Ioannidis JPA (2008) Why most discovered true associations are inflated. *Epidemiology, 19*, 640-648.

In fact, I’d go one step further and say that low power is an excellent reason for why a study should be *desk rejected* by an editor. An editor has many jobs, but one of those is to elevate or maintain the quality of the work that the journal publishes. Given how poorly our research is holding up, you really need a good excuse to publish underpowered research because doing so will detract from the reputation of the journal in our evolving climate. For example, if you are studying a rare group or your resources are limited you may have some justification for using low power designs. But if that is the case, you need to be careful about using inferential statistics. The study may have to justified as being descriptive or suggestive, at best. On the other hand, if you are a researcher at a major university with loads of resources like grant monies, a big subject pool, and an army of undergraduate RAs, there is little or no justification for producing low-powered research. Low power studies simply increase the noise in the system making it harder and harder to figure out whether an effect exists or not and whether a theory has any merit. Given how many effects are failing to replicate, we have to start taking power seriously unless we want to see our entire field go down in replicatory flames.

Another reason to be skeptical of low powered studies is that, if researchers are using significance testing as a way of screening the veracity of their results, they can only detect medium to large effects. Given the fact that on average most of our effects are small, using low powered research makes you a victim of the “streetlight effect”—you know, where the drunk person only looks for their keys under the streetlight because that is the only place they can see? That is not an ideal way of doing science.

**Budlie Bond**: Ok, I can see some of your points. And, thanks to some of those online power calculators, I can see how I can plan my studies to ensure a high degree of power. But how do power calculations work in more complex designs, like those that use structural equation modeling or multi-level models?

**Prof. Belfry-Roaster**. There is less consensus on how to think about power in these situations. But it is still possible to make educated decisions, even without technical expertise. For example, even in a design that involves both repeated measures and between-person factors, the between-persons effects still involve comparisons across people and should be powered accordingly. And in SEM applications, if the pairwise covariances are not estimated with precision, there are lots of ways for those errors to propagate and create estimation problems for the model.

Thankfully, there are some very smart people out there and they have done their best to provide some benchmarks and power calculation programs for more complex designs. You can find some of them here.

**Budlie Bond**: I wasn’t sure how to think about power when I conducted my first study. But, in looking back at my data, I see that, given the sample size I used, my power to detect the effect size I found (d = .50) was over 90%. Does that mean my study was highly powered?

**Prof. Belfry-Roaster**: When power is computed based on the effect size observed, the calculation is sometimes referred to as *post hoc power* or *observed power*. Although there can be value in computing post hoc power, it is not a good way to estimate the power of your design for a number of reasons. We have touched on some of those already. For example, if the design is based on a small sample, only large effects (true large effects and overestimates of smaller or null effects) will cross the p < .05 barrier. As a result, the effects you see will tend to be larger than the population effects of interest, leading to inflated power estimates.

More importantly, however, power is a design issue, not a data-analytic issue. Ideally, you want to design your studies to be capable of detecting the effects that matter for the theory of interest. Thus, when designing a study, you should always ask “How many subjects do I need to have 80% power to detect an effect if the population effect size is X or higher,” where X is the minimum effect size of interest. This value is likely to vary from one investigator to another, but given that small effects matter for most directional theories, it is prudent to set this value fairly low.

You can also ask about the power of the design in a post hoc way, but it is best to ask not what the power was to detect the effect that was observed, but to ask what the power was to detect effects of various sizes. For example, if you conducted a two-condition study with 50 people per cell, you had 17% power to detect a d of .20, 51% to detect a d of .40, and 98% to detect a d of .80. In short, you can evaluate the power of a study to detect population effects of various sizes after the fact. But you don’t want to compute post hoc power by asking what the power of the design was for detecting the effect observed. For more about these issues, please see Daniel Lakens great blog post on post-hoc power: http://daniellakens.blogspot.com/2014/12/observed-power-and-what-to-do-if-your.html

**Budlie Bond**: Thanks for all of the background on power. I got in a heated discussion with Chip again and he said a few things that made me think you are emphasizing power too much. First he said that effect sizes are for applied researchers and that his work is theoretical. The observed effect sizes are not important because they depend on a number of factors that can vary from one context to the next (e.g., the strength of the manipulation, the specific DV measured). Are effect sizes and power less useful in basic research than they are in applied research?

**Prof. Belfry-Roaster**: With the exception of qualitative research, all studies have effect sizes, even if they are based on contrived or artificial conditions (think of Harlow’s wire monkeys, for example). If researchers want a strong test of their theory in highly controlled laboratory settings, they gain enormously by considering power and thus effect sizes. They need that information to design the study to test their idea well.

Moreover, if other people want to replicate your technique or build on your design, then it is really helpful if they know the effect size that you found so they can plan accordingly.

In short, even if the effect size doesn’t naturally translate into something of real world significance given the nature of the experimental or lab task, there is an effect size associated with the task. Knowing it is important not only for properly testing the theory and seeing what kinds of factors can modulate the effect, but for helping others plan their research accordingly. You are not only designing better research by using effect sizes, you are helping other researchers too.

Another reason to always estimate your effect sizes is that they are a great reality check on the likelihood and believability of your results. For example, when we do individual difference research, we start thinking that we are probably measuring the same thing when the correlation between our independent and dependent variable gets north of .50. Well, a correlation of .5 is like a d-score of .8. So, if you are getting effect sizes above .5 or above a d of .8 your findings warrant a few skeptical questions. First, you should ask whether you measured the same thing twice. In an experiment d’s around 1 should really be the exclusive domain of manipulation checks, not an outcome of some subtle manipulation. Second, you have to ask yourself how you are the special one who found the “low hanging fruit” that is implicit in a huge effect size. We’ve been at the study of psychology for many decades. How is it that you are the genius who finally hit on a relationship that is so large that it should visible to the naked eye (Jacob Cohen’s description of a medium effect size) and all of the other psychologists missed it? Maybe you are that observant, but it is a good question to ask yourself nonetheless.

And this circles back to our discussion of low power. Small N studies only have enough power to detect medium to large effect sizes with any reliability. If you insist on running small N studies and ignore your effect sizes, you are more likely to produce inaccurate results simply because you can’t detect anything but large effects, which we know are rare. If you then report those exaggerated effect sizes, other people who attempt to build on your research will plan their designs around an effect that is too large. This will lead them to underpower their studies and fail to replicate your results. The underpowered study thus sets in motion a series of unfortunate events that lead to confusion and despair rather than progress.

Choosing to ignore your effect sizes in the context of running small N studies is like sticking your head in the sand. Don’t do it.

**Budlie Bond**: Chip’s advisor also says we should not be so concerned with Type 1 errors. What do you think?

**Prof. Belfry-Roaster:** To state out loud that you are not worried about Type 1 errors at this point in time is inconceivable. Our studies are going down in flames one-by-one. The primary reason for that is because we didn’t design the original studies well—typically they were underpowered and never directly replicated. If we continue to turn a blind eye to powering our research well, we are committing to a future where our research will repeatedly not replicate. Personally, I don’t want you to experience that fate.

**Budlie Bond**: Chip also said that some people argue against using large samples because doing so is cheating. You are more likely to get a statistically significant finding that is really tiny. By only running small studies they say they protect themselves from promoting tiny effects.

**Prof. Belfry-Roaster**: While it is true that small studies can’t detect small effects, the logic of this argument does not add up. The only way this argument would hold is if you didn’t identify the effect size in your study, which, unfortunately, used to be quite common. Researchers used to and still do obsess over p-values. In a world where you only use p-values to decide whether a theory or hypothesis is true, it is the case that large samples will allow you to claim that an effect holds when it is actually quite small. On the other hand, if you estimate your effect sizes in all of your studies then there is nothing deceptive about using a large sample. Once you identify an effect as small, then other researchers can decide for themselves whether they think it warrants investment. Moreover, the size of the sample is independent of the effect size (or should be). You can find a big effect size with a big sample too.

Ultimately, the benefits of a larger sample outweigh the costs of a small sample. You gain less sampling variance and a more stable estimate of the effect size. In turn, the test of your idea should hold up better in future research than the results from a small N study. That’s nothing to sneeze at.

You can also see how this attitude toward power and effect sizes creates a vicious cycle. If you use small N studies evaluated solely by p-values rather than power and effect sizes, you are destined to lead a chaotic research existence where findings come and go, seemingly nonsensically. If you then argue that 1) all theories are not true under certain conditions, or that 2) the manipulation is delicate, or 3) that there are loads of hidden moderators, you can quickly get into a situation where your claims cannot be refuted. Using high powered studies with effect size estimates can keep you a little more honest about the viability of your ideas.

**Budlie Bond**: Chip’s advisor says all of this obsession with power is hindering our ability to be creative. What do you think?

**Prof. Belfry-Roaster**: Personally, I believe the only thing standing between you and a creative idea is gray matter and some training. How you go about testing that idea is not a hindrance to coming up with the idea in the first place. At the moment we don’t suffer from a deficit of creativity. Rather we have an excess of creativity combined with the deafening roar of noise pollution. The problem with low powered studies is they simply add to the noise. But how valuable are creative ideas in science if they are not true?

Many researchers believe that the best way to test creative ideas is to do so quickly with few people. Actually, it is the opposite. If you really want to know whether your new, creative idea is a good one, you want to overpower your study. One reason is that low power leads to Type II errors—not detecting an effect when the null is false. That’s a tragedy. And, it is an easy tragedy to avoid—just power your study adequately.

Creative ideas are a dime a dozen. But creative ideas based on robust statistical evidence are rare indeed. Be creative, but be powerfully creative.

**Budlie Bond**: Some of the other grad students were saying that the sample sizes you are proposing are crazy large. They don’t want to run studies that large because they won’t be able to keep up with grad students who can crank out a bunch of small studies and publish at a faster rate.

**Prof. Belfry-Roaster**: I’m sympathetic to this problem as it does seem to indicate that research done well will inevitably take more time, but I think that might be misleading. If your fellow students are running low powered studies, they are likely finding mixed results, which given our publication norms won’t get a positive reception. Therefore, to get a set of studies all with p-values below .05 they will probably end up running multiple small studies. In the end, they will probably test as many subjects as you’ll test in your one study. The kicker is that their work will also be less likely to hold up because it is probably riddled with Type 1 errors.

Will Gervais has conducted some interesting simulations comparing research strategies that focus on slower, but more powerful studies against those that focus on faster, less powerful samples. His analysis suggests that you’re not necessarily better off doing a few quick and under-powered studies. His post is worth a read.

http://willgervais.com/blog/2016/2/10/casting-a-wide-net

**Budlie Bond**: Chip says that your push for large sample sizes also discriminates against people who work at small colleges and universities because they don’t have access to the numbers of people you need to run adequately-powered research.

**Prof. Belfry-Roaster**: He’s right. Running high powered studies will require potentially painful changes to the way we conduct research. This, as you know, is one reason why we often offer up our lab to friends at small universities to help conduct their studies. But they also should not be too distraught. There are creative and innovative solutions to the necessity of running well-designed studies (e.g., high powered research). First, we can take inspiration from the GWAS researchers. When faced with the reality that they couldn’t go it alone, they combined efforts into a consortium in order to do their science properly. There is nothing stopping researchers at both smaller and larger colleges and universities from creating their own consortia. It might mean we have to change our culture of worshiping the “hero” researcher, but that’s okay. Two or more heads is always better than one (at least according to most groups research. I wonder how reliable that work is…?). Second, we are on the verge of technological advances that can make access to large numbers of people much easier—MtTurk being just one example. Third, some of our societies, like SPSP and APS and APA are rich. Well, rich enough to consider doing something creative with their money. They could, if they had the will and the leadership, start thinking about doing proactive things like creating subject pool panels that we can all access and run our studies on and thus conduct better powered research.

Basically Bud, we are at a critical juncture. We can continue doing things the old way which means we will continue to produce noisy, unreplicable research, or we can change for the better. The simplest and most productive thing we can do so is to increase the power of our research. In most cases, this can be achieved simply by increasing the average sample size of our studies. That’s why we obsess about the power of the research we read and evaluate. Any other questions?

Great post, thank you!

“First, we can take inspiration from the GWAS researchers. When faced with the reality that they couldn’t go it alone, they combined efforts into a consortium in order to do their science properly.”

If I am not mistaken, there is an initiative underway for psychology (?) where you can ask for cooperation concerning your research. Please check out: https://osf.io/view/studyswap/

Honest admission, I love it and I hate it.

I love it because it is a great introduction to the concept of statistical power and why it is so important to think about power of studies. Love it. Really great. Super important. Must be widely shared.

I hate it because it doesn’t mention me. Oh yes, my ego is bruised. It hurts. For two years I slaved on publishing a paper on power and apparently it is not worthwhile mentioning. Apparently, the issue of planning more than one study is too complex for this basic introduction to the importance of power.

So, I added Part II

Budlie Bond:

So, I get it know power is a good thing because I want to show that personality changes and if I have low power because personality changes are small, I end up with a strong significant result for the stable part of personality and a non-significant result for my predictor of change. Now, my data look as if personality is stable even though I strongly believe it is changing. But now some researchers like Brent W. Roberts are asking for replication studies. So, I wonder if I need to do two studies to show a significant result in the original study and in the replication study, how do I make sure I have enough power to get significant results in both studies? I am also working with another professor in experimental social psychology on a paper for JPSP and if it gets rejected PSPB or JESP. These journals want at least three significant results before they believe a result. Is it enough to have 80% power in each study?

Prof. Belfry-Roaster:

Good question Budlie. If you need more than one significant result, you need to have more power in each study. This is because the power to get significant results in a set of studies is lower than the power of each individual study. Schimmack (2012) called this total power. See, if you have 80% power in one study, the chance to get significant results in two studies is only 64%, or .80 * .80 * 100. It is like flipping a coin where a coin flip is a study with 50% power. If you flip a coin twice, your chance to get head on both trials is only 25%. If you try three times, your chance of getting head is only .5 * .5 * .5 = 12.5%. Now would you want to invest resources in a set of studies where you only have a 12.5% chance to be successful? No. So, you need to have more power in each study to end up with 80% power for a set of studies?

Budlie Bond:

Sure, but how much power do I need in each study to have high, what’s it called again, total power?

Prof. Belfry-Roaster:

Easy, you reverse the calculation. Rather than starting with power of a single study and then computing total power, you start with total power and compute the power of each study. See, the formula for total power is a power function [chuckle], no pun intended. Power functions raise a number to the power of another number. If we want to compute total power, we take power and raise it by the number of studies. What software are you using?

Budlie Bond: Hm… I’d rather not say; SPSS, but I am learning R now. R is so cool.

Prof. Belfry-Roaster:

I think in SPSS, you write compute TP = Power**k where Power is power of a single study and k is the number of studies. For two studies with 80% power you would write .80**2.

Budlie Bond:

Sorry, I only do point and click in SPSS. My graduate courses didn’t teach me syntax.

Prof. Belfry-Roaster: Yeah, I know. Sucks, but that is why you are learning R now. So, just use R. You just write .80^2 on the command prompt line and it will give you the right answer, .64. For three studies, you write .80^3 and you get total power for three studies. To go from total power to power, you just have to change the number of studies to 1 divided by number of studies. Type .80^(1/2) and you get the power you need in each study to have total power of 80% for a pair of studies. Don’t forget the brackets. Otherwise you just divide power by number of studies and you get nonsense.

Budlie Bond:

Wow, it’s that easy?

Prof. Belfry-Roaster:

Yeah, but nobody does it. I haven’t seen an a priori power analysis for total power ever.

Budlie Bond:

Then how do authors manage to be successful? I mean, I heard that many studies are underpowered and if total power is even lower, it seems impossible to get so many significant results.

Prof. Belfry-Roaster:

True, you are a quick learner. Of course, they are not always successful. They just don’t mention the studies that produced a non-significant result.

Budlie Bond:

But isn’t that fraud?

Prof. Belfry-Roaster:

No. Actually researchers sometimes include these studies, but editors ask them to remove them. After all, the other studies showed the effect, so not including a study or two that showed a non-significant result is not a big deal.

Budlie Bond:

But then I am throwing away a whole study or even several studies with non-significant results. Isn’t that a waste of resources. Wouldn’t it be better to plan studies so that I have good total power and don’t have to through away data from studies with non-significant results?

Prof. Belfry-Roaster:

Yes. Or you can just not test for statistical significance in each study or include studies with non-significant results and show that the effect is there in a meta-analysis of your studies. This is what this Schimmack guy recommended. Some journals now allow you to do this. One paper even reported 14 non-significant results and then showed the effect was there in a meta-analysis. Of course, you can also just send it to one of these new pay to publish journals if your adviser enough grant money to pay for it.

Budlie Bond:

So, I don’t really need 80% total power. I don’t even need 80% power in each study, if it is only necessary to show significance in a meta-analysis?

Prof. Belfry-Roaster:

Yes. You just do a power analysis with the total sample size across all of your two or three, or how many studies and make sure you have good power to get significance.

Budlie Bond: So, if my power analysis shows that I need 200 participants to get significance, I could do two studies with N = 100 and it doesn’t matter whether they are significant, as long as I get significance in a meta-analysis? Then what is the difference between doing two studies with N = 100 or one study with N = 200?

Prof. Belfry-Roaster:

I don’t know. You may want to ask Brent W. Roberts, if he says you need an exact replication study to show the effect is real.

Reblogged this on Statistics and Substance use and commented:

The power of power…

This is a great and very useful post!

However there are two things I do have to quibble with.

1.

“However, for other types of analyses, like interaction effects, some smart people have estimated that you’ll need more than twice as many participants—in the range of 500.”Contrary to an apparently popular belief, there is nothing inherent about interactions among categorical predictors that makes them harder to detect than main/simple effects. You go on to say “Uri Simonsohn has shown that if you want to demonstrate that a manipulation can make a previously demonstrated effect go away, you need twice as many participants as you would need to demonstrate the original main effect” — which is true, as Uri proved, but note that this is NOT a statement about interaction effects generally requiring more participants to detect. It is a statement about the power to detect a very special type of interaction effect, roughly, one that “makes a previously demonstrated effect go away”, as you say.

One simple argument for why there can’t possibly be anything special about interactions that makes them harder to detect than main effects is to note that it’s basically arbitrary which of the effects in the experiment we want to think of as interactions and which as main effects in the first place. Ultimately these are all just columns of values in the design matrix. This point is easily illustrated in a 2×2 factorial example, where we have dyadic interactions among two participants, person A and person B, both of whom are either male or female. So our contrast matrix, where the rows are the groups and the columns are the contrasts (not including the intercept) might look like:

A_gender B_gender same_sex

A_male,B_male 1 1 1

A_male,B_female 1 -1 -1

A_female,B_male -1 1 -1

A_female,B_female -1 -1 1

Here we view the main effects as being the gender of person A and the gender of person B, and their interaction is the effect of A and B being the same sex. Right off the bat we can see that, assuming equal group sizes, the contrasts all have the same variance (half +1 values and half -1 values), so already it’s difficult to see how one could be inherently easier or harder to detect than the other. Okay, now depending on our research question, same_sex might be the effect of interest, in which case we may want a model where same_sex is one of the predictors (not computed as a product), and then we just add the 2 other codes that will give us a complete orthogonal set. But we can get this by just rearranging the contrast matrix from above:

same_sex A_gender B_gender

A_male,B_male 1 1 1

A_female,B_female 1 -1 -1

A_male,B_female -1 1 -1

A_female,B_male -1 -1 1

Here we view same_sex as being one of the main effects. But this is the same contrast matrix, just with rows and columns rearranged, so it leads to exactly the same design matrix! Surely it would be absurd to suppose that the same_sex effect has somehow become easier to detect, or say the B_gender effect harder to detect (because it’s the product of same_sex and A_gender), just because we changed our minds about which columns of the design matrix are “main effects” and which are “interactions”?

2.

“My office-mate Chip Harkel says that there is a new rule of thumb that you should simply get 50 people per cell in an experiment. Is that a sensible strategy to use when I don’t know what the effect size might be?”You rightly point out here that following such a rule may not be the greatest idea. But you don’t mention what I think is the more fundamental problem with the rule, which is that in factorial designs (which is usually what we’re talking about in experimental psychology — and including 2-group designs here as a special case of factorial), it is not the per-cell sample size that matters for power, it is the total sample size. Rules of thumb based on the sample sizes per cell don’t make nearly as much sense as rules of thumb based on total sample size, because they lead to wildly different levels of power for designs with different numbers of cells.

To illustrate the point, consider two experiments, each with N = 128 total subjects. Experiment 1 uses a 2×2 design, so it has 32 per cell. Experiment 2 uses a 2x2x2x2 design, so it has 8 per cell. In both cases, the effect of interest is one of the main effects, and these two main effects have the same effect size — let’s say we’re talking about the standardized effect size partial eta-squared. These two studies have essentially identical power to detect the main effect of interest (technically there’s a small difference due to different denominator degrees of freedom), even though Experiment 1 has four times as many subjects per cell as Experiment 2. The reason is that they both have the same total number of subjects, and that is what matters for power (in a factorial design). Clearly if we’re going to use sample size rules of thumb at all, they should be based on the total sample size.

Both of these points #1 and #2 are discussed in more detail at the following pages:

http://jakewestfall.org/blog/index.php/2015/05/26/think-about-total-n-not-n-per-cell/

http://jakewestfall.org/blog/index.php/2015/05/27/follow-up-what-about-uris-2n-rule/

https://methodology.psu.edu/ra/most/femiscon

Apparently using the HTML “code” tag does NOT preserve spaces, so the tables of contrasts still ended up coming out badly formatted….sigh

Some additional resources about observed power can be found here.

https://replicationindex.wordpress.com/tag/observed-power/

Terrific!

Are interaction effects harder to find?

I agree with jake987722.

Power is a function of effect size. However, this has implications for some interactions.

If I am predicting that an effect exists in one group with effect size d = .5 and does not exist in another group, meaning effect size is d = 0, I have an effect size of d =.25 for my main effect power analysis across samples, but for my interaction effect I have to show that d = .5 is different from d = 0.

Take, Bem’s (2011) study. Effect size for psi = .25, but effect for extraverts is supposed to be d = .5 and effect for introverts is zero. What is the power of demonstrating a mean difference of d = .5 vs. 0 in a comparison of two samples, relative to the one-sample test of d = .25 in a one-sample t-test?

Bem already calculated that N = 100 gives 80% power for d = .25 in one-sample t-test. Power for the interaction effect that shows difference between extraverts (d = .5) and introverts (d = 0) with n = 50 per group (total N = 100) is 70%.

We don’t need interactions to show that the n = 50 per cell rule does not ensure good power. Between-subject design with d = .2 (small effect) requires N > 700 (n > 350 per cell) to have 80% power.

“Knowledge about power is power” to get significant, credible, and replicable results. I hope this blog posts contributes to the growing awareness about the importance of power and I hope somewhere in heaven Jacob Cohen is smiling.

These are very nice technical comments about the interactions. We did not elaborate on those issues for several reasons, but one is probably paramount, though I don’t have much data to support it. I suspect if you bothered to do a meta-analysis of interaction effects alone, you would find the aggregate effect size to be smaller than the d of .4. One could extract the interaction effects from the Replication Report for example and estimate the average effect size there. I suspect in might be very close to zero. So, to Jake’s point, a simple rule of thumb is that as your effect size goes down your sample size demands rise.

I’m curious to learn more about when the total sample size matters, and when the sample size per cell matters. From my experience reading the literature, it’s fairly common for researchers to want to do more specific comparisons beyond the overall test of the factorial design. Is it correct that in cases when researchers want to compare two cells, or subsets of cells, within a larger factorial design, then it becomes relevant what the sample size per cell is? If so, I suspect this applies to many studies with factorial designs (but of course this is an empirical question).

Hi Simine, the general rule is that what matters for the power to detect a particular contrast is, roughly, the number of observations involved in that contrast and the variance of the contrast values. By focusing here on 2^k type factorials like 2×2, 2x2x2, etc., we hold constant the variance of the contrast values, just for simplicity’s sake. In a 2^k factorial experiment, the usual “factorial questions” one asks about the cell means all involve the entire dataset, and so they have the same power given the same effect size. But if you ask about comparisons among individual cells of the factorial, these generally won’t involve all of the data — in the most extreme case, they might involve the data from only 2 of the cells — so power will be lower for that test. Presumably if one has run a factorial experiment, this means that the factorial questions are the ones of primary interest. But as you say, it does depend on the case at hand — if one of your primary research questions is not a factorial question but a question about one or more of the simple effects, then you’d generally need a greater sample size to have sufficient power for that test (and in fact you might consider not bothering with running the full factorial).

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This is an excellent overview of social scientists’ struggle with statistical power, but what emerges from it is that social scientists largely equate ‘more power’ with ‘larger samples’. While sample size is a big part of the equation, there are other ways of increasing your power, and it may be worthwhile to explore those more than has been the case.

However, I think that the near-universal use of standardised effect sizes (Cohen’s d, Pearson’s r) precludes discussions of these other ways of achieving greater power.

To clarify, statistical power is a function of raw/unstandardised effect size (i.e., expressed in the units measured), residual error, and sample size. Cohen’s d and Pearson’s r combine the raw/unstandardised effect size and the residual error (or more specifically, within-group variability) into one measure, such that you can increase your standardised effect size by studying larger effects or by decreasing within-group variability. When studying a given phenomenon, the former may be out of your hands, but you often can accomplish the latter, as I’ll discuss later. When using canned standardised effect sizes, however, two between-subjects experiments with 60 participants investigating the exact same phenomenon will both be considered to have pretty abysmal power to detect an effect size of d = 0.5 – even though one experiment may have excellent chances to detect the effect by virtue of having achieved low residual variability whereas the other may have dreadful chances of detecting the same raw effect size. My suggestion is to do away with these standardised effect sizes in order to foster discussions about other ways to improve power, which could centre around these two questions:

1. How can we improve the precision of our variables? More accurate measures (as opposed to quick and dirty measures) will, by definition, reduce the error with which the constructs of interest are measured and, in consequence, reduce the residual variability, thereby increasing power.

2. How can we take into account known sources of variability at the design stage? It’s not sample heterogeneity per se that determines power, but rather heterogeneity that hasn’t been accounted for. We probably can do a better job of identifying likely sources of variation among participants and use this information to our advantage by (a) reducing the scope of the participant sample (this’ll jeopardise external validity even more, though), (b) using covariates, including pretests (they’ve got a bad rep at the moment, but when used correctly, one or two carefully chosen covariates can work wonders power-wise), (c) using blocking. Other strategies include the more wide-spread adoption of within-subject designs (a recurring theme on Andrew Gelman’s blog), even if it means coming to terms with transfer effects, and taking multiple measurements of the outcome variable per participants (cue mixed-effects models).

TL;DR: Not all 60-participant between-participant studies are equal power-wise.

(Incidentally, how useful are statements about the average effect size in a field given problems with replicability, p-hacking etc.? Just wondering, I probably should read those papers again.)

Doubled down there on your comment. These are great points about improving the precision of studies in ways other than increasing N. The within-subjects approach has been a standard of cognitive science for decades to good effect.

As for your parenthetical about the statements about average effect sizes drawn from field wide reviews, we were being generous. None of those reviews corrects for potential bias. If you did you would arrive at a much smaller average effect size and a much larger sample size requirement. We didn’t want to completely depress Bud.

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Excellent and very helpful….many thanks. Have passed along to our graduate students. One minor correction: According to Cohen (1992), a medium, not a large, effect size is the threshold at which an effect becomes visible to the naked eye. Thanks again for the user-friendly and enjoyable tutorial.

Duly noted and the essay has been revised for accuracy. Three cheers for post-publication peer review! That should teach us not to write from our shoddy memory….

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