Tag Archives: NHST

Peer-Reviews from Psychological Methods

Power, Z-Curve, Zcurve, , , , ,
Times are changing. Media are flooded with fake news and journals are filled with fake novel discoveries. The only way to fight bias and fake information is full transparency and openness.
Jerry Brunner and I wrote a paper that examined the validity of z-curve, the method underlying powergraphs, to Psychological Methods.As soon as we submitted it, we made the manuscript and the code available. Nobody used the opportunity to comment on the manuscript. Now we got the official reviews.

We would like to thank the editor and reviewers for spending time and effort on reading (or at least skimming) our manuscript and writing comments.  Normally, this effort would be largely wasted because like many other authors we are going to ignore most of their well-meaning comments and suggestions and try to publish the manuscript mostly unchanged somewhere else. As the editor pointed out, we are hopeful that our manuscript will eventually be published because 95% of written manuscripts get eventually published. So, why change anything.  However, we think the work of the editor and reviewers deserves some recognition and some readers of our manuscript may find them valuable. Therefore, we are happy to share their comments for readers interested in replicabilty and our method of estimating replicability from test statistics in original articles.

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Dear Dr. Brunner,

I have now received the reviewers’ comments on your manuscript. Based on their analysis and my own evaluation, I can no longer consider this manuscript for publication in Psychological Methods. There are two main reasons that I decided not to accept your submission. The first deals with the value of your statistical estimate of replicability. My first concern is that you define replicability specifically within the context of NHST by focusing on power and p-values. I personally have fewer problems with NHST than many methodologists, but given the fact that the literature is slowly moving away from this paradigm, I don’t think it is wise to promote a method to handle replicability that is unusable for studies that are conducted outside of it. Instead of talking about replicability as estimating the probability of getting a significant result, I think it would be better to define it in more continuous terms, focusing on how similar we can expect future estimates (in terms of effect sizes) to be to those that have been demonstrated in the prior literature. I’m not sure that I see the value of statistics that specifically incorporate the prior sample sizes into their estimates, since, as you say, these have typically been inappropriately low.

Sure, it may tell you the likelihood of getting significant results if you conducted a replication of the average study that has been done in the past. But why would you do that instead of conducting a replication that was more appropriately powered?

Reviewer 2 argues against the focus on original study/replication study distinction, which would be consistent with the idea of estimating the underlying distribution of effects, and from there selecting sample sizes that would produce studies of acceptable power. Reviewer 3 indicates that three of the statistics you discussed are specifically designed for single studies, and are no longer valid when applied to sets of studies, although this reviewer does provide information about how these can be corrected.

The second main reason, discussed by Reviewer 1, is that although your statistics may allow you to account for selection biases introduced by journals not accepting null results, they do not allow you to account for selection effects prior to submission. Although methodologists will often bring up the file drawer problem, it is much less of an issue than people believe. I read about a survey in a meta-analysis text (I unfortunately can’t remember the exact citation) that indicated that over 95% of the studies that get written up eventually get published somewhere. The journal publication bias against non-significant results is really more an issue of where articles get published, rather than if they get published. The real issue is that researchers will typically choose not to write up results that are non-significant, or will suppress non-significant findings when writing up a study with other significant findings. The latter case is even more complicated, because it is often not just a case of including or excluding significant results, but is instead a case where researchers examine the significant findings they have and then choose a narrative that makes best use of them, including non-significant findings when they are part of the story but excluding them when they are irrelevant. The presence of these author-side effects means that your statistic will almost always be overestimating the actual replicability of a literature.

The reviewers bring up a number of additional points that you should consider. Reviewer 1 notes that your discussion of the power of psychological studies is 25 years old, and therefore likely doesn’t apply. Reviewer 2 felt that your choice to represent your formulas and equations using programming code was a mistake, and suggests that you stick to standard mathematical notation when discussing equations. Reviewer 2 also felt that you characterized researcher behaviors in ways that were more negative than is appropriate or realistic, and that you should tone down your criticisms of these behaviors. As a grant-funded researcher, I can personally promise you that a great many researchers are concerned about power,since you cannot receive government funding without presenting detailed power analyses. Reviewer 2 noted a concern with the use of web links in your code, in that this could be used to identify individuals using your syntax. Although I have no suspicions that you are using this to keep track of who is reviewing your paper, you should remove those links to ensure privacy. Reviewer 1 felt that a number of your tables were not necessary, and both reviewers 2 and 3 felt that there were parts of your writing that could be notably condensed. You might consider going through the document to see if you can shorten it while maintaining your general points. Finally, reviewer 3 provides a great many specific comments that I feel would greatly enhance the validity and interpretability of your results. I would suggest that you attend closely to those suggestions before submitting to another journal.

For your guidance, I append the reviewers’ comments below and hope they will be useful to you as you prepare this work for another outlet.

Thank you for giving us the opportunity to consider your submission.

Sincerely, Jamie DeCoster, PhD
Associate Editor
Psychological Methods

Reviewers’ comments:

Reviewer #1:

The goals of this paper are admirable and are stated clearly here: “it is desirable to have an alternative method of estimating replicability that does not require literal replication. We see this method as complementary to actual replication studies.”

However, I am bothered by an assumption of this paper, which is that each study has a power (for example, see the first two paragraphs on page 20). This bothers me for several reasons. First, any given study in psychology will often report many different p-values. Second, there is the issue of p-hacking or forking paths. The p-value, and thus the power, will depend on the researcher’s flexibility in analysis. With enough researcher degrees of freedom, power approaches 100% no matter how small the effect size is. Power in a preregistered replication is a different story. The authors write, “Selection for significance (publication bias) does not change the power values of individual studies.” But to the extent that there is selection done _within_ a study–and this is definitely happening–I don’t think that quoted sentence is correct.

So I can’t really understand the paper as it is currently written, as it’s not clear to me what they are estimating, and I am concerned that they are not accounting for the p-hacking that is standard practice in published studies.

Other comments:

The authors write, “Replication studies ensure that false positives will be promptly discovered when replication studies fail to confirm the original results.” I don’t think “ensure” is quite right, since any replication is itself random. Even if the null is true, there is a 5% chance that a replication will confirm just by chance. Also many studies have multiple outcomes, and if any appears to be confirmed, this can be taken as a success. Also, replications will not just catch false positives, they will also catch cases where the null hypothesis is false but where power is low. Replication may have the _goal_ of catching false positives, but it is not so discriminating.

The Fisher quote, “A properly designed experiment rarely fails to give …significance,” seems very strange to me. What if an experiment is perfectly designed, but the null hypothesis happens to be true? Then it should have a 95% chance of _not_ giving significance.

The authors write, “Actual replication studies are needed because they provide more information than just finding a significant result again. For example, they show that the results can be replicated over time and are not limited to a specific historic, cultural context. They also show that the description of the original study was sufficiently precise to reproduce the study in a way that it successfully replicated the original result.” These statements seem too strong to me. Successful replication is rejection of the null, and this can happen even if the original study was not described precisely, etc.

The authors write, “A common estimate of power is that average power is about 50% (Cohen 1962, Sedlmeier and Gigerenzer 1989). This means that about half of the studies in psychology have less than 50% power.” I think they are confusing the mean with the median here. Also I would guess that 50% power is an overestimate. For one thing, psychology has changed a lot since 1962 or even 1989 so I see no reason to take this 50% guess seriously.

The authors write, “We define replicability as the probability of obtaining the same result in an exact replication study with the same procedure and sample sizes.” I think that by “exact” they mean “pre-registered” but this is not clear. For example, suppose the original study was p-hacked. Then, strictly speaking, an exact replication would also be p-hacked. But I don’t think that’s what the authors mean. Also, it might be necessary to restrict the definition to pre-registered studies with a single test. Otherwise there is the problem that a paper has several tests, and any rejection will be taken as a successful replication.

I recommend that the authors get rid of tables 2-15 and instead think more carefully about what information they would like to convey to the reader here.

Reviewer #2:

This paper is largely unclear, and in the areas where it is clear enough to decipher, it is unwise and unprofessional.

This study’s main claim seems to be: “Thus, statistical estimates of replicability and the outcome of replication studies can be seen as two independent methods that are expected to produce convergent evidence of replicability.” This is incorrect. The approaches are unrelated. Replication of a scientific study is part of the scientific process, trying to find out the truth. The new study is not the judge of the original article, its replicability, or scientific contribution. It is merely another contribution to the scientific literature. The replicator and the original article are equals; one does not have status above the other. And certainly a statistical method applied to the original article has no special status unless the method, data, or theory can be shown to be an improvement on the original article.

They write, “Rather than using traditional notation from Statistics that might make it difficult for non-statisticians to understand our method, we use computer syntax as notation.” This is a disqualifying stance for publication in a serious scholarly journal, and it would an embarrassment to any journal or author to publish these results. The point of statistical notation is clarity, generality, and cross-discipline understanding. Computer syntax is specific to the language adopted, is not general, and is completely opaque to anyone who uses a different computer language. Yet everyone who understands their methods will have at least seen, and needs to understand, statistical notation. Statistical (i.e., mathematical) notation is the one general language we have that spans the field and different fields. No computer syntax does this. Proofs and other evidence are expressed in statistical notation, not computer syntax in the (now largely unused) S statistical language. Computer syntax, as used in this paper, is also ill-defined in that any quantity defined by a primitive function of the language can change any time, even after publication, if someone changes the function. In fact, the S language, used in this paper, is not equivalent to R, and so the authors are incorrect that R will be more understandable. Not including statistical notation, when the language of the paper is so unclear and self-contradictory, is an especially unfortunate decision. (As it happens I know S and R, but I find the manuscript very difficult to understand without imputing my own views about what the authors are doing. This is unacceptable. It is not even replicable.) If the authors have claims to make, they need to state them in unambiguous mathematical or statistical language and then prove their claims. They do not do any of these things.

It is untrue that “researchers ignore power”. If they do, they will rarely find anything of interest. And they certainly write about it extensively. In my experience, they obsess over power, balancing whether they will find something with the cost of doing the experiment. In fact, this paper misunderstands and misrepresents the concept: Power is not “the long-run probability of obtaining a statistically significant result.” It is the probability that a statistical test will reject a false null hypothesis, as the authors even say explicitly at times. These are very different quantities.

This paper accuses “researchers” of many other misunderstandings. Most of these are theoretically incorrect or empirically incorrect.One point of the paper seems to be “In short, our goal is to estimate average power of a set of studies with unknown population effect sizes that can assume any value, including zero.” But I don’t see why we need to know this quantity or how the authors’ methods contribute to us knowing it. The authors make many statistical claims without statistical proofs, without any clear definition of what their claims are, and without empirical evidence. They use simulation that inquires about a vanishingly small portion of the sample space to substitute for an infinite domain of continuous parameter values; they need mathematical proofs but do not even state their claims in clear ways that are amenable to proof.

No coherent definition is given of the quantity of interest. “Effect size” is not generic and hypothesis tests are not invariant to the definition, even if it is true that they are monotone transformations of each other. One effect size can be “significant” and a transformation of the effect size can be “not significant” even if calculated from the same data. This alone invalidates the authors’ central claims.

The first 11.5 pages of this paper should be summarized in one paragraph. The rest does not seem to contribute anything novel. Much of it is incorrect as well. Better to delete throat clearing and get on with the point of the paper.

I’d also like to point out that the authors have hard-coded URL links to their own web site in the replication code. The code cannot be run without making a call to the author’s web site, and recording the reviewer’s IP address in the authors’ web logs. Because this enables the authors to track who is reviewing the manuscript, it is highly inappropriate. It also makes it impossible to replicate the authors results. Many journals (and all federal grants) have prohibitions on this behavior.

I haven’t checked whether Psychological Methods has this rule, but the authors should know better regardless.

Reviewer 3

Review of “How replicable is psychology? A comparison of four methods of estimating replicability on the bias of test statistics in original studies”

It was my pleasure to review this manuscript. The authors compare four methods of estimating replicability. One undeniable strength of the general approach is that these measures of replicability can be computed before or without actually replicating the study/studies. As such, one can see the replicability measure of a set of statistically significant findings as an index of trust in these findings, in the sense that the measure provides an estimate of the percentage of these studies that is expected to be statistically significant when replicating them under the same conditions and same sample size (assuming the replication study and the original study assess the same true effect). As such, I see value in this approach. However, I have many comments, major and minor, which will enable the authors to improve their manuscript.

Major comments

1. Properties of index.

What I miss, and what would certainly be appreciated by the reader, is a description of properties of the replicability index. This would include that it has a minimum value equal to 0.05 (or more generally, alpha), when the set of statistically significant studies has no evidential value. Its maximum value equals 1, when the power of studies included in the set was very large. A value of .8 corresponds to the situation where statistical power of the original situation was .8, as often recommended. Finally, I would add that both sample size and true effect size affect the replicability index; a high value of say .8 can be obtained when true effect size is small in combination with a large sample size (you can consider giving a value of N, here), or with a large true effect size in combination with a small sample size (again, consider giving values).

Consider giving a story like this early, e.g. bottom of page 6.

2. Too long explanations/text

Perhaps it is a matter of taste, but sometimes I consider explanations much too long. Readers of Psychological Methods may be expected to know some basics. To give you an example, the text on page 7 in “Introduction of Statistical Methods for Power estimation” is very long. I believe its four paragraphs can be summarized into just one; particularly the first one can be summarized in one or two sentences. Similarly, the section on “Statistical Power” can be shortened considerably, imo. Other specific suggestions for shortening the text, I mention below in the “minor comments” section. Later on I’ll provide one major comment on the tables, and how to remove a few of them and how to combine several of them.

3. Wrong application of ML, p-curve, p-uniform

This is THE main comment, imo. The problem is that ML (Hedges, 1984), p-curve, p-uniform, enable the estimation of effect size based on just ONE study. Moreover,  Simonsohn (p-curve) as well as the authors of p-uniform would argue against estimating the average effect size of unrelated studies. These methods are meant to meta-analyze studies on ONE topic.

4. P-uniform and p-curve section, and ML section

This section needs a major revision. First, I would start the section with describing the logic of the method. Only statistically significant results are selected. Conditional on statistical significance, the methods are based on conditional p-values (not just p-values), and then I would provide the formula on top of page 18. Most importantly, these techniques are not constructed for estimating effect size of a bunch of unrelated studies. The methods should be applied to related studies. In your case, to each study individually. See my comments earlier.

Ln(p), which you use in your paper, is not a good idea here for two reasons: (1) It is most sensitive to heterogeneity (which is also put forward by Van Assen et al (2014), and (2) applied to single studies it estimates effect size such that the conditional p-value equals 1/e, rather than .5  (resulting in less nice properties).

The ML method, as it was described, focuses on estimating effect size using one single study (see Hedges, 1984). So I was very surprised to see it applied differently by the authors. Applying ML in the context of this paper should be the same as p-uniform and p-curve, using exactly the same conditional probability principle. So, the only difference between the three methods is the method of optimization. That is the only difference.

You develop a set-based ML approach, which needs to assume a distribution of true effect size. As said before, I leave it up to you whether you still want to include this method. For now, I have a slight preference to include the set-based approach because it (i) provides a nice reference to your set-based approach, called z-curve, and (ii) using this comparison you can “test” how robust the set-based ML approach is against a violation of the assumption of the distribution of true effect size.

Moreover, I strongly recommend showing how their estimates differ for certain studies, and include this in a table. This allows you to explain the logic of the methods very well. Here a suggestion. I would provide the estimates of four methods (…) for p-values .04, .025, .01, .001, and perhaps .0001). This will be extremely insightful. For small p-values, the three methods’ estimates will be similar to the traditional estimate. For p-values > .025, the estimate will be negative, for p = .025 the estimate will be (close to) 0. Then, you can also use these same studies and p-values to calculate the power of a replication study (R-index).

I would exclude Figure 1, and the corresponding text. Is not (no longer) necessary.

For the set-based ML approach, if you still include it, please explain how you get to the true value distribution (g(theta)).

5a. The MA set, and test statistics

Many different effect sizes and test statistics exist. Many of them can be transformed to ONE underlying parameter, with a sensible interpretation and certain statistical properties. For instance, the chi2, t, and F(1,df) can all be transformed to d or r, and their SE can be derived. In the RPP project and by John et al (2016) this is called the MA set. Other test statistics, such as F(>1, df) cannot be converted to the same metric, and no SE is defined on that metric. Therefore, the statistics F(>1,df) were excluded from the meta-analyses in the RPP  (see the supplementary materials of the RPP) and by Johnson et al (2016) and also Morey and Lakens (2016), who also re-analyzed the data of the RPP.

Fortunately, in your application you do not estimate effect size but only estimate power of a test, which only requires estimating the ncp and not effect size. So, in principle you can include the F(>1,df) statistics in your analyses, which is a definite advantage. Although I can see you can incorporate it for the ML, p-curve, p-uniform approach, I do not directly see how these F(>1,df) statistics can be used for the two set-based methods (ML and z-curve); in the set-based methods, you put all statistics on one dimension (z) using the p-values. How do you defend this?

5b. Z-curve

Some details are not clear to me, yet. How many components (called r in your text) are selected, and why? Your text states: “First, select a ncp parameter m ; . Then generate Z from a normal distribution with mean m ; I do not understand, since the normal distribution does not have an ncp. Is it that you nonparametrically model the distribution of observed Z, with different components?

Why do you use kernel density estimation? What is it’s added value? Why making it more imprecise by having this step in between? Please explain.

Except for these details, procedure and logic of z-curve are clear

6. Simulations (I): test statistics

I have no reasons, theoretical or empirical, why the analyses would provide different results for Z, t, F(1,df), F(>1,df), chi2. Therefore, I would omit all simulation results of all statistics except 1, and not talk about results of these other statistics. For instance, in the simulations section I would state that results are provided on each of these statistics but present here only the results of t, and of others in supplementary info. When applying the methods to RPP, you apply them to all statistics simultaneously, which you could mention in the text (see also comment 4 above).

7. mean or median power (important)

One of my most important points is the assessment of replicability itself. Consider a set of studies for which replicability is calculated, for each study. So, in case of M studies, there are M replicability indices. Which statistics would be most interesting to report, i.e., are most informative? Note that the distribution of power is far some symmetrical, and actually may be bimodal with modes at 0.05 and 1.  For that reason alone, I would include in any report of replicability in a field the proportion of R-indices equal to 0.05 (which amounts to the proportion of results with .025 < p < .05) and the proportion of R-indices equal to 1.00 (e.g., using two decimals, i.e. > .995). Moreover, because power values are recommend of .8 or more, I also could include the proportion of studies with power > .8.

We also would need a measure of central tendency. Because the distribution is not symmetric, and may be skewed, I recommend using the median rather than the mean. Another reason to use the median rather than the mean is because the mean does not provide useable information on whether methods are biased or not, in the simulations. For instance, if true effect size = 0, because of sampling error the observed power will exceed .05 in exactly 50% of the cases (this is the case for p-uniform; since with probability .5 the p-value will exceed .025) and larger than .05 in the other 50% of the cases. Hence, the median will be exactly equal to .05, whereas the mean will exceed .05. Similarly, if true effect size is large the mean power will be too small (distribution skewed to the left). To conclude, I strongly recommend including the median in the results of the simulation.

In a report, such as for the RPP later on in the paper, I recommend including (i)

p(R=.05), (ii) p(R >= .8), (iii) p(R>= .995), (iv) median(R), (v) sd(R), (vi)

distribution R, (vii) mean R. You could also distinguish this for soc psy and cog psy.

8. simulations (II): selection of conditions

I believe it is unnatural to select conditions based on “mean true power” because we are most familiar with effect size and their distribution, and sample sizes and their distribution. I recommend describing these distributions, and then the implied power distribution (surely the median value as well, not or not only the mean).

9.  Omitted because it could reveal identity of reviewer

10. Presentation of results

I have comments on what you present, on how you present the results. First, what you present. For the ML and p-methods, I recommend presenting the distribution of R in each of the conditions (at least for fixed true effect size and fixed N, where results can be derived exactly relatively easy). For the set-based methods, if you focus on average R (which I do not recommend, I recommend median R), then present the RMSE. The absolute median error is minimized when you use the median. So, average-RMSE is a couple, and median-absolute error is a couple.

Now the presentation of results. Results of p-curve/p-uniform/ML are independent of the number of tests, but set-based methods (your ML variant) and z-curve are not.

Here the results I recommend presenting:

Fixed effect size, heterogeneity sample size

**For single-study methods, the probability distribution of R (figure), including mean(R), median(R), p(R=.05), p(R>= .995), sd(R). You could use simulation for approximating this distribution. Figures look like those in Figure 3, to the right.

**Median power, mean/sd as a function of K

**Bias for ML/p-curve/p-uniform amounts to the difference between median of distribution and the actual median, or the difference between the average of the distribution and the actual average. Note that this is different from set-based methods.

**For set-based methods, a table is needed (because of its dependence on k).

Results can be combined in one table (i.e., 2-3, 5-6, etc)

Significance tests comparing methods

I would exclude Table 4, Table 7, Table 10, Table 13. These significance tests do not make much sense. One method is better than another, or not – significance should not be relevant (for a very large number of iterations, a true difference will show up). You could simply describe in the text which method works best.

Heterogeneity in both sample size and effect size

You could provide similar results as for fixed effect size (but not for chi2, or other statistics). I would also use the same values of k as for the fixed effect case. For the fixed effect case you used 15, 25, 50, 100, 250. I can imagine using as values of k for both conditions k = 10, 30, 100, 400, 2,000 (or something).

Including the k = 10 case is important, because set-based methods will have more problems there, and because one paper or a meta-analysis or one author may have published just one or few statistically significant effect sizes. Note, however, that k=2,000 is only realistic when evaluating a large field.

Simulation of complex heterogeneity

Same results as for fixed effect size and heterogeneity in both sample size and effect size. Good to include a condition where the assumption of set-based ML is violated. I do not yet see why a correlation between N and ES may affect the results. Could you explain? For instance, for the ML/p-curve/p-uniform methods, all true effect sizes in combination with N result in a distribution of R for different studies; how this distribution is arrived at, is not relevant, so I do not yet see the importance of this correlation. That is, this correlation should only affect the results through the distribution of R. More reasoning should be provided, here.

Simulation of full heterogeneity

I am ambivalent about this section. If test statistic should not matter, then what is the added value of this section? Other distributions of sample size may be incorporated in previous section “complex heterogeneity”;. Other distributions of true effect may also be incorporated in the previous section. Note that Johnson et al (2016) use the RPP data to estimate that 90% of effects in psychology estimate a true zero effect. You assume only 10%.

Conservative bootstrap

Why only presenting the results of z-curve? By changing the limits of the interval, the interpretation becomes a bit awkward; what kind of interval is it now? Most importantly, coverages of .9973 or .9958 are horrible (in my opinion, these coverages are just as bad as coverages of .20). I prefer results of 95% confidence intervals, and then show their coverages in the table. Your &lsquo;conservative&rsquo; CIs are hard to interpret. Note also that this is paper on statistical properties of the methods, and one property is how well the methods perform w.r.t. 95% CI.

By the way, examining 95% CI of the methods is very valuable.

11. RPP

In my opinion, this section should be expanded substantially. This is where you can finally test your methodology, using real data! What I would add is the following: **Provide the distribution of R (including all statistics mentioned previously, i.e. p(R=0.05), p(R >= .8), p(R >= .995), median(R), mean(R), sd(R), using single-study methods **Provide previously mentioned results for soc psy and cog psy separately **Provide results of z-curve, and show your kernel density curve (strange that you never show this curve, if it is important in your algorithm).  What would be really great, is if you predict the probability of replication success (power) using the effect size estimate based on the original effect size estimated (derived from a single study) and the N of the replication sample. You could make a graph with on the X-axis this power, and on the Y-axis the result of the replication. Strong evidence in favor of your method would be if your result better predicts future replicability than any other index (see RPP for what they tried). Logistic regression seems to be the most appropriate technique for this.

Using multiple logistic regression, you can also assess if other indices have an added value above your predictions.

To conclude, for now you provide too limited results to convince readers that your approach is very useful.

Minor comments

P4 top: “heated debates” A few more sentence on this debate, including references to those debates would be fair. I would like to mention/recommend the studies of Maxwell et al (2015) in American Psychologist, the comment on the OSF piece in Science, and its response, and the very recent piece of Valen E Johnson et al (2016).

P4, middle: consider starting a new paragraph at “Actual replication”; In the sentence after this one, you may add “or not”;.

Another advantage of replication is that it may reveal heterogeneity (context dependence). Here, you may refer to the ManyLabs studies, which indeed reveal heterogeneity in about half of the replicated effects. Then, the next paragraph may start with “At the same time” To conclude, this piece starting with “Actual replication”; can be expanded a bit

P4, bottom,  “In contrast”; This and the preceding sentence is formulated as if sampling error does not exist. It is much too strong! Moreover, if the replication study had low power, sampling error is likely the reason of a statistically insignificant result. Here you can be more careful/precise. The last sentence of this paragraph is perfect.

P5, middle: consider adding more refs on estimates of power in psychology, e.g. Bakker and Wicherts 35% and that study on neuroscience with power estimates close to 20%. Last sentence of the same paragraph; assuming same true effect and same sample size.

P6, first paragraph around Rosenthal. Consider referring to the study of Johson et al (2016), who used a Bayesian analysis to estimate how many non-significant studies remain unpublished.

P7, top: &ldquo;studies have the same power (homogenous case) “(heterogenous case). This is awkward. Homogeneity and heterogeneity is generally reserved for variation in true effect size. Stick to that. Another problem here is that “heterogeneous”; power can be created by “heterogeneity”; in sample size and/or heterogeneity in effect size. These should be distinguished, because some methods can deal with heterogeneous power caused by heterogeneous N, but not heterogeneous true effect size. So, here, I would simple delete the texts between brackets.

P7, last sentence of first paragraph; I do not understand the sentence.

P10, “average power”. I did not understand this sentence.

P10, bottom: Why do you believe these methods to be most promising?

P11, 2nd par: Rephrase this sentence. Heterogeneity of effect size is not because of sampling variation. Later in this paragraph you also mix up heterogeneity with variation in power again. Of course, you could re-define heterogeneity, but I strongly recommend not doing so (in order not to confuse others); reserve heterogeneity to heterogeneity in true effect size.

P11, 3rd par, 1st sentence: I do not understand this sentence. But then again, this sentence may not be relevant (see major comments), because for applying p-uniform and p-curve heterogeneity of effect size is not relevant.

P11 bottom: maximum likelihood method. This sentence is not specific enough. But then again, this sentence may not be relevant (see major comments).

P12: Statistics without capital.

P12: “random sampling distribution”; delete “random”;. By the way, I liked this section on Notation and statistical background.

Section “Two populations of power”;. I believe this section is unnecessarily long, with a lot of text. Consider shortening. The spinning wheel analogy is ok.

P16, “close to the first” You mean second?

P16, last paragraph, 1st sentence: English?

Principle 2: The effect on what? Delete last sentence in the principle.

P17, bottom: include the average power after selection in your example.

p-curve/p-uniform: modify, as explained in one of the major comments.

P20, last sentence: Modify the sentence – the ML approach has excellent properties asymptotically, but not sample size is small. Now it states that it generally yields more precise estimates.

P25, last sentence of 4. Consider deleting this sentence (does not add anything useful).

P32: “We believe that a negative correlation between” some part of sentence is missing.

P38, penultimate sentence: explain what you mean by “decreasing the lower limit by .02”; and “increasing the upper limit by .02”;.

The Association for Psychological Science Improves Success Rate from 95% to 100% by Dropping Hypothesis Testing: The Sample Mean is the Sample Mean, Type-I Error 0%

NHST, Psychology, Replication, Statistics, , , , , , , , , ,

The editor of Psychological Science published an Editorial with the title “Business Not as Usual.” (see also Observer interview and new Submission Guidelines) The new submission guidelines recommend the following statistical approach.

Effective January 2014, Psychological Science recommends the use of the “new statistics”—effect sizes, confidence intervals, and meta-analysis—to avoid problems associated with null-hypothesis significance testing (NHST). Authors are encouraged to consult this Psychological Science tutorial by Geoff Cumming, which shows why estimation and meta-analysis are more informative than NHST and how they foster development of a cumulative, quantitative discipline. Cumming has also prepared a video workshop on the new statistics that can be found here.

The editorial is a response to the current crisis in psychology that many findings cannot be replicated and the discovery that numerous articles in Psychological Science show clear evidence of reporting biases that lead to inflated false-positive rates and effect sizes (Francis, 2013).

The editorial is titled “Business not as usual.”  So what is the radical response that will ensure increased replicability of results published in Psychological Science? One solution is to increase transparency and openness to discourage the use of deceptive research practices (e.g., not publishing undesirable results or selective reporting of dependent variables that showed desirable results). The other solution is to abandon null-hypothesis significance testing.

Problem of the Old Statistics: Researchers had to demonstrate that their empirical results could have occurred only with a 5% probability if there is no effect in the population.

Null-hypothesis testing has been the main method to relate theories to empirical data. An article typically first states a theory and then derives a theoretical prediction from the theory. The theoretical prediction is then used to design a study that can be used to test the theoretical prediction. The prediction is tested by computing the ratio of the effect size and sampling error (signal-to-noise) ratio. The next step is to determine the probability of obtaining the observed signal-to-noise ratio or an even more extreme one under the assumption that the true effect size is zero. If this probability is smaller than a criterion value, typically p < .05, the results are interpreted as evidence that the theoretical prediction is true. If the probability does not meet the criterion, the data are considered inconclusive.

However, non-significant results are irrelevant because Psychological Science is only interested in publishing research that supports innovative novel findings. Nobody wants to know that drinking fennel tea does not cure cancer, but everybody wants to know about a treatment that actually cures cancer. So, the main objective of statistical analyses was to provide empirical evidence for a predicted effect by demonstrating that an obtained result would occur only with a 5% probability if the hypothesis were false.

Solution to the problem of Significance Testing: Drop the Significance Criterion. Just report your sample mean and the 95% confidence interval around it.

NoNeedForNull

Eich claims that “researchers have recognized,…, essential problems with NHST in general, and with dichotomous thinking (“significant” vs. “non-significant” ) thinking it engenders in particular. It is true that statisticians have been arguing about the best way to test theoretical predictions with empirical data. In fact, they are still arguing. Thus, it is interesting to examine how Psychological Science found a solution to the elusive problem of statistical inference. The answer is to avoid statistical inferences altogether and to avoid dichotomous thinking. Does fennel tea cure cancer? Maybe, 95%CI d = -.4 to d = +4. No need to test for statistical significance. No need to worry about inadequate sample sizes. Just do a study and report your sample means with a confidence interval. It is that easy to fix the problems of psychological science.

The problem is that every study produces a sample mean and a confidence interval. So, how do the editors of Psychological Science pick the 5% of submitted manuscripts that will be accepted for publication? Eich lists three criteria.

  1. What will the reader of this article learn about psychology that he or she did not know (or could not have known) before?

The effect of manipulation X on dependent variable Y is d = .2, 95%CI = -.2 to .6. We can conclude from this result that it is unlikely that the manipulation leads to a moderate decrease or a strong increase in the dependent variable Y.

  1. Why is that knowledge important for the field?

The finding that the experimental manipulation of Y in the laboratory is somewhat more likely to produce an increase than a decrease, but could also have no effect at all has important implications for public policy.

  1. How are the claims made in the article justified by the methods used?

The claims made in this article are supported by the use of Cumming’s New Statistics. Based on a precision analysis, the sample size was N = 100 (n = 50 per condition) to achieve a precision of .4 standard deviations. The study was preregistered and the data are publicly available with the code to analyze the data (SPPS t-test groups x (1,2) / var y.).

If this sounds wrong to you and you are a member of APS, you may want to write to Erich Eich and ask for some better guidelines that can be used to evaluate whether a sample mean or two or three or four sample means should be published in your top journal.

A Critical Review of Cumming’s (2014) New Statistics: Reselling Old Statistics as New Statistics

Power, Psychological Science, Research Integrity, Statistics, , , , , , , ,

Cumming (2014) wrote an article “The New Statistics: Why and How” that was published in the prestigious journal Psychological Science.   On his website, Cumming uses this article to promote his book “Cumming, G. (2012). Understanding The New Statistics: Effect Sizes, Confidence Intervals, and Meta-Analysis. New York: Routledge.”

The article clear states the conflict of interest. “The author declared that he earns royalties on his book (Cumming, 2012) that is referred to in this article.” Readers are therefore warned that the article may at least inadvertently give an overly positive account of the new statistics and an overly negative account of the old statistics. After all, why would anybody buy a book about new statistics when the old statistics are working just fine.

This blog post critically examines Cumming’s claim that his “new statistics” can solve endemic problems in psychological research that have created a replication crisis and that the old statistics are the cause of this crisis.

Like many other statisticians who are using the current replication crisis as an opportunity to sell their statistical approach, Cumming’s blames null-hypothesis significance testing (NHST) for the low credibility of research articles in Psychological Science (Francis, 2013).

In a nutshell, null-hypothesis significance testing entails 5 steps. First, researchers conduct a study that yields an observed effect size. Second, the sampling error of the design is estimated. Third, the ratio of the observed effect size and sampling error (signal-to-noise ratio) is computed to create a test-statistic (t, F, chi-square). The test-statistic is then used to compute the probability of obtaining the observed test-statistic or a larger one under the assumption that the true effect size in the population is zero (there is no effect or systematic relationship). The last step is to compare the test statistic to a criterion value. If the probability (p-value) is less than a criterion value (typically 5%), the null-hypothesis is rejected and it is concluded that an effect was present.

Cumming’s (2014) claims that we need a new way to analyze data because there is “renewed recognition of the severe flaws of null-hypothesis significance testing (NHST)” (p. 7). His new statistical approach has “no place for NHST” (p. 7). His advice is to “whenever possible, avoid using statistical significance or p values” (p. 8).

So what is wrong with NHST?

The first argument against NHST is that Ioannidis (2005) wrote an influential article with the eye-catching title “Why most published research findings are false” and most research articles use NHST to draw inferences from the observed results. Thus, NHST seems to be a flawed method because it produces mostly false results. The problem with this argument is that Ioannidis (2005) did not provide empirical evidence that most research findings are false, nor is this a particularly credible claim for all areas of science that use NHST, including partical physics.

The second argument against NHST is that researchers can use questionable research practices to produce significant results. This is not really a criticism of NHST, because researchers under pressure to publish are motivated to meet any criteria that are used to select articles for publication. A simple solution to this problem would be to publish all submitted articles in a single journal. As a result, there would be no competition for limited publication space in more prestigious journals. However, better studies would be cited more often and researchers will present their results in ways that lead to more citations. It is also difficult to see how psychology can improve its credibility by lowering standards for publication. A better solution would be to ensure that researchers are honestly reporting their results and report credible evidence that can provide a solid empirical foundation for theories of human behavior.

Cummings agrees. “To ensure integrity of the literature, we must report all research conducted to a reasonable standard, and reporting must be full and accurate” (p. 9). If a researcher conducted five studies with only a 20% chance to get a significant result and would honestly report all five studies, p-values would provide meaningful evidence about the strength of the evidence, namely most p-values would be non-significant and show that the evidence is weak. Moreover, post-hoc power analysis would reveal that the studies had indeed low power to test a theoretical prediction. Thus, I agree with Cumming’s that honesty and research integrity are important, but I see no reason to abandon NHST as a systematic way to draw inferences from a sample about the population because researchers have failed to disclose non-significant results in the past.

Cumming’s then cites a chapter by Kline (2014) that “provided an excellent summary of the deep flaws in NHST and how we use it” (p. 11). Apparently, the summary is so excellent that readers are better off by reading the actual chapter because Cumming’s does not explain what these deep flaws are. He then observes that “very few defenses of NHST have been attempted” (p. 11). He doesn’t even list a single reference. Here is one by a statistician: “In defence of p-values” (Murtaugh, 2014). In a response, Gelman agrees that the problem is more with the way p-values are used rather than with the p-value and NHST per se.

Cumming’s then states a single problem of NHST. Namely that it forces researchers to make a dichotomous decision. If the signal-to-noise ratio is above a criterion value, the null-hypothesis is rejected and it is concluded that an effect is present. If the signal-to-noise ratio is below the criterion value the null-hypothesis is not rejected. If Cumming’s has a problem with decision making, it would be possible to simply report the signal-to-noise ratio or simply to report the effect size that was observed in a sample. For example, mortality in an experimental Ebola drug trial was 90% in the control condition and 80% in the experimental condition. As this is the only evidence, it is not necessary to compute sampling error, signal-to-noise ratios, or p-values. Given all of the available evidence, the drug seems to improve survival rates. But wait. Now a dichotomous decision is made based on the observed mean difference and there is no information about the probability that the results in the drug trial generalize to the population. Maybe the finding was a chance finding and the drug actually increases mortality. Should we really make life-and-death decision if the decision were based on the fact that 8 out of 10 patients died in one condition and 9 out of 10 patients died in the other condition?

Even in a theoretical research context decisions have to be made. Editors need to decide whether they accept or reject a submitted manuscript and readers of published studies need to decide whether they want to incorporate new theoretical claims in their theories or whether they want to conduct follow-up studies that build on a published finding. It may not be helpful to have a fixed 5% criterion, but some objective information about the probability of drawing the right or wrong conclusions seems useful.

Based on this rather unconvincing critique of p-values, Cumming’s (2014) recommends that “the best policy is, whenever possible, not to use NHST at all” (p. 12).

So what is better than NHST?

Cumming then explains how his new statistics overcome the flaws of NHST. The solution is simple. What is astonishing about this new statistic is that it uses the exact same components as NHST, namely the observed effect size and sampling error.

NHST uses the ratio of the effect size and sampling error. When the ratio reaches a value of 2, p-values reach the criterion value of .05 and are considered sufficient to reject the null-hypothesis.

The new statistical approach is to multiple the standard error by a factor of 2 and to add and subtract this value from the observed mean. The interval from the lower value to the higher value is called a confidence interval. The factor of 2 was chosen to obtain a 95% confidence interval.  However, drawing a confidence interval alone is not sufficient to draw conclusions from the data. Whether we describe the results in terms of a ratio, .5/.2 = 2.5 or in terms of a 95%CI = .5 +/- .2 or CI = .1 to .7, is not a qualitative difference. It is simply different ways to provide information about the effect size and sampling error. Moreover, it is arbitrary to multiply the standard error by a factor of 2. It would also be possible to multiply it by a factor of 1, 3, or 5. A factor of 2 is used to obtain a 95% confidence interval rather than a 20%, 50%, 80%, or 99% confidence interval. A 95% confidence is commonly used because it corresponds to a 5% error rate (100 – 95 = 5!). A 95% confidence interval is as arbitrary as a p-value of .05.

So, how can a p-value be fundamentally wrong and how can a confidence interval be the solution to all problems if they provide the same information about effect size and sampling error? In particular how do confidence intervals solve the main problem of making inferences from an observed mean in a sample about the mean in a population?

To sell confidence intervals, Cumming’s uses a seductive example.

“I suggest that, once freed from the requirement to report p values, we may appreciate how simple, natural, and informative it is to report that “support for Proposition X is 53%, with a 95% CI of [51, 55],” and then interpret those point and interval estimates in practical terms” (p 14).

Support for proposition X is a rather unusual dependent variable in psychology. However, let us assume that Cumming refers to an opinion poll among psychologists whether NHST should be abandoned. The response format is a simple yes/no format. The average in the sample is 53%. The null-hypothesis is 50%. The observed mean of 53% in the sample shows more responses in favor of the proposition. To compute a significance test or to compute a confidence interval, we need to know the standard error. The confidence interval ranges from 51% to 55%. As the 95% confidence interval is defined by the observed mean plus/minus two standard errors, it is easy to see that the standard error is SE = (53-51)/2 = 1% or .01. The formula for the standard error in a one sample test with a dichotomous dependent variable is sqrt(p * (p-1) / n)). Solving for n yields a sample size of N = 2,491. This is not surprising because public opinion polls often use large samples to predict election outcomes because small samples would not be informative. Thus, Cumming’s example shows how easy it is to draw inferences from confidence intervals when sample sizes are large and confidence intervals are tight. However, it is unrealistic to assume that psychologists can and will conduct every study with samples of N = 1,000. Thus, the real question is how useful confidence intervals are in a typical research context, when researchers do not have sufficient resources to collect data from hundreds of participants for a single hypothesis test.

For example, sampling error for a between-subject design with N = 100 (n = 50 per cell) is SE = 2 / sqrt(100) = .2. Thus, the lower and upper limit of the 95%CI are 4/10 of a standard deviation away from the observed mean and the full width of the confidence interval covers 8/10th of a standard deviation. If the true effect size is small to moderate (d = .3) and a researcher happens to obtain the true effect size in a sample, the confidence interval would range from d = -.1 to d = .7. Does this result support the presence of a positive effect in the population? Should this finding be published? Should this finding be reported in newspaper articles as evidence for a positive effect? To answer this question, it is necessary to have a decision criterion.

One way to answer this question is to compute the signal-to-noise ratio, .3/.2 = 1.5 and to compute the probability that the positive effect in the sample could have occurred just by chance, t(98) = .3/.2 = 1.5, p = .15 (two-tailed). Given this probability, we might want to see stronger evidence. Moreover, a researcher is unlikely to be happy with this result. Evidently, it would have been better to conduct a study that could have provided stronger evidence for the predicted effect, say a confidence interval of d = .25 to .35, but that would have required a sample size of N = 6,500 participants.

A wide confidence interval can also suggest that more evidence is needed, but the important question is how much more evidence is needed and how narrow a confidence interval should be before it can give confidence in a result. NHST provides a simple answer to this question. The evidence should be strong enough to reject the null-hypothesis with a specified error rate. Cumming’s new statistics provides no answer to the important question. The new statistics is descriptive, whereas NHST is an inferential statistic. As long as researchers merely want to describe their data, they can report their results in several ways, including reporting of confidence intervals, but when they want to draw conclusions from their data to support theoretical claims, it is necessary to specify what information constitutes sufficient empirical evidence.

One solution to this dilemma is to use confidence intervals to test the null-hypothesis. If the 95% confidence interval does not include 0, the ratio of effect size / sampling error is greater than 2 and the p-value would be less than .05. This is the main reason why many statistics programs report 95%CI intervals rather than 33%CI or 66%CI. However, the use of 95% confidence intervals to test significance is hardly a new statistical approach that justifies the proclamation of a new statistic that will save empirical scientists from NHST. It is NHST! Not surprisingly, Cumming’s states that “this is my least preferred way to interpret a confidence interval” (p. 17).

However, he does not explain how researchers should interpret a 95% confidence interval that does include zero. Instead, he thinks it is not necessary to make a decision. “We should not lapse back into dichotomous thinking by attaching any particular importance to whether a value of interest lies just inside or just outside our CI.”

Does an experimental treatment for Ebolay work? CI = -.3 to .8. Let’s try it. Let’s do nothing and do more studies forever. The benefit of avoiding making any decisions is that one can never make a mistake. The cost is that one can also never claim that an empirical claim is supported by evidence. Anybody who is worried about dichotomous thinking might ponder the fact that modern information processing is built on the simple dichotomy of 0/1 bits of information and that it is common practice to decide the fate of undergraduate students on the basis of scoring multiple choice tests in terms of True or False answers.

In my opinion, the solution to the credibility crisis in psychology is not to move away from dichotomous thinking, but to obtain better data that provide more conclusive evidence about theoretical predictions and a simple solution to this problem is to reduce sampling error. As sampling error decreases, confidence intervals get smaller and are less likely to include zero when an effect is present and the signal-to-noise ratio increases so that p-values get smaller and smaller when an effect is present. Thus, less sampling error also means less decision errors.

The question is how small should sampling error be to reduce decision error and at what point are resources being wasted because the signal-to-noise ratio is clear enough to make a decision.

Power Analysis

Cumming’s does not distinguish between Fischer’s and Neyman-Pearson’s use of p-values. The main difference is that Fischer advocated the use of p-values without strict criterion values for significance testing. This approach would treat p-values just like confidence intervals as continuous statistics that do not imply an inference. A p-value of .03 is significant with a criterion value of .05, but it is not significant with a criterion value of .01.

Neyman-Pearson introduced the concept of a fixed criterion value to draw conclusions from observed data. A criterion value of p = .05 has a clear interpretation. It means that a test of 1,000 null-hypotheses is expected to produce about 50 significant results (type-I errors). A lower error rate can be achieved by lowering the criterion value (p < .01 or p < .001).

Importantly, Neyman-Pearson also considered the alternative problem that the p-value may fail to reach the critical value when an effect is actually present. They called this probability the type-II error. Unfortunately, social scientists have ignored this aspect of Neyman-Pearson Significance Testing (NPST). Researchers can avoid making type-II errors by reducing sampling error. The reason is that a reduction of sampling error increases the signal-to-noise ratio.

For example, the following p-values were obtained from simulating studies with 95% power. The graph only shows p-values greater than .001 to make the distribution of p-values more prominent. As a result 62.5% of the data are missing because these p-values are below p < .001. The histogram of p-values has been popularized by Simmonsohn et al. (2013) as a p-curve. The p-curve shows that p-values are heavily skewed towards low p-values. Thus, the studies provide consistent evidence that an effect is present, even though p-values can vary dramatically from one study (p = .0001) to the next (p = .02). The variability of p-values is not a problem for NPST as long as the p-values lead to the same conclusion because the magnitude of a p-value is not important in Neyman-Pearson hypothesis testing.

CumFig1

The next graph shows p-values for studies with 20% power. P-values vary just as much, but now the variation covers both sides of the significance criterion, p = .05. As a result, the evidence is often inconclusive and 80% of studies fail to reject the false null-hypothesis.

CumFig2

R-Code
seed = length(“Cumming’sDancingP-Values”)
power=.20
low_limit = .000
up_limit = .10
p <-(1-pnorm(rnorm(2500,qnorm(.975,0,1)+qnorm(.20,0,1),1),0,1))*2
hist(p,breaks=1000,freq=F,ylim=c(0,100),xlim=c(low_limit,up_limit))
abline(v=.05,col=”red”)
percent_below_lower_limit = length(subset(p, p <  low_limit))/length(p)
percent_below_lower_limit
If a study is designed to test a qualitative prediction (an experimental manipulation leads to an increase on an observed measure), power analysis can be used to plan a study so that it has a high probability of providing evidence for the hypothesis if the hypothesis is true. It does not matter whether the hypothesis is tested with p-values or with confidence intervals by showing that the confidence does not include zero.

Thus, power analysis seems useful even for the new statistics. However, Cummings is “ambivalent about statistical power” (p. 23). First, he argues that it has “no place when we use the new statistics” (p. 23), presumably because the new statistics never make dichotomous decisions.

Cumming’s next argument against power is that power is a function of the type-I error criterion. If the type-I error probability is set to 5% and power is only 33% (e.g., d = .5, between-group design N = 40), it is possible to increase power by increasing the type-I error probability. If type-I error rate is set to 50%, power is 80%. Cumming’s thinks that this is an argument against power as a statistical concept, but raising alpha to 50% is equivalent to reducing the width of the confidence interval by computing a 50% confidence interval rather than a 95% confidence interval. Moreover, researchers who adjust alpha to 50% are essentially saying that the null-hypothesis would produce a significant result in every other study. If an editor finds this acceptable and wants to publish the results, neither power analysis nor the reported results are problematic. It is true that there was a good chance to get a significant result when a moderate effect is present (d = .5, 80% probability) and when no effect is present (d = 0, 50% probability). Power analysis provides accurate information about the type-I and type-II error rates. In contrast, the new statistics provides no information about error rates in decision making because it is merely descriptive and does not make decisions.

Cumming then points out that “power calculations have traditionally been expected [by granting agencies], but these can be fudged” (p. 23). The problem with fudging power analysis is that the requested grant money may be sufficient to conduct the study, but insufficient to produce a significant result. For example, a researcher may be optimistic and expect a strong effect, d = .80, when the true effect size is only a small effect, d = .20. The researcher conducts a study with N = 52 participants to achieve 80% power. In reality the study has only 11% power and the researcher is likely to end up with a non-significant result. In the new statistics world this is apparently not a problem because the researcher can report the results with a wide confidence interval that includes zero, but it is not clear why a granting agency should fund studies that cannot even provide information about the direction of an effect in the population.

Cummings then points out that “one problem is that we never know true power, the probability that our experiment will yield a statistically significant result, because we do not know the true effect size; that is why we are doing the experiment!” (p. 24). The exclamation mark indicates that this is the final dagger in the coffin of power analysis. Power analysis is useless because it makes assumptions about effect sizes when we can just do an experiment to observe the effect size. It is that easy in the world of new statistics. The problem is that we do not know the true effect sizes after an experiment either. We never know the true effect size because we can never determine a population parameter, just like we can never prove the null-hypothesis. It is only possible to estimate population parameter. However, before we estimate a population parameter, we may simply want to know whether an effect exists at all. Power analysis can help in planning studies so that the sample mean shows the same sign as the population mean with a specified error rate.

Determining Sample Sizes in the New Statistics

Although Cumming does not find power analysis useful, he gives some information about sample sizes. Studies should be planned to have a specified level of precision. Cumming gives an example for a between-subject design with n = 50 per cell (N = 100). He chose to present confidence intervals for unstandardized coefficients. In this case, there is no fixed value for the width of the confidence interval because the sampling variance influences the standard error. However, for standardized coefficients like Cohen’s d, sampling variance will produce variation in standardized coefficients, while the standard error is constant. The standard error is simply 2 / sqrt (N), which equals SE = .2 for N = 100. This value needs to be multiplied by 2 to get the confidence interval, and the 95%CI = d +/- .4.   Thus, it is known before the study is conducted that the confidence interval will span 8/10 of a standard deviation and that an observed effect size of d > .4 is needed to exclude 0 from the confidence interval and to state with 95% confidence that the observed effect size would not have occurred if the true effect size were 0 or in the opposite direction.

The problem is that Cumming provides no guidelines about the level of precision that a researcher should achieve. Is 8/10 of a standard deviation precise enough? Should researchers aim for 1/10 of a standard deviation? So when he suggests that funding agencies should focus on precision, it is not clear what criterion should be used to fund research.

One obvious criterion would be to ensure that precision is sufficient to exclude zero so that the results can be used to state that direction of the observed effect is the same as the direction of the effect in the population that a researcher wants to generalize to. However, as soon as effect sizes are used in the planning of the precision of a study, precision planning is equivalent to power analysis. Thus, the main novel aspect of the new statistics is to ignore effect sizes in the planning of studies, but without providing guidelines about desirable levels of precision. Researchers should be aware that N = 100 in a between-subject design gives a confidence interval that spans 8/10 of a standard deviation. Is that precise enough?

Problem of Questionable Research Practices, Publication Bias, and Multiple Testing

A major problem for any statistical method is the assumption that random sampling error is the only source of error. However, the current replication crisis has demonstrated that reported results are also systematically biased. A major challenge for any statistical approach, old or new, is to deal effectively with systematically biased data.

It is impossible to detect bias in a single study. However, when more than one study is available, it becomes possible to examine whether the reported data are consistent with the statistical assumption that each sample is an independent sample and that the results in each sample are a function of the true effect size and random sampling error. In other words, there is no systematic error that biases the results. Numerous statistical methods have been developed to examine whether data are biased or not.

Cumming (2014) does not mention a single method for detecting bias (Funnel Plot, Eggert regression, Test of Excessive Significance, Incredibility-Index, P-Curve, Test of Insufficient Variance, Replicabiity-Index, P-Uniform). He merely mentions a visual inspection of forest plots and suggests that “if for example, a set of studies is distinctly too homogeneous – it shows distinctly less bouncing around than we would expect from sampling variability… we can suspect selection or distortion of some kind” (p. 23). However, he provides no criteria that explain how variability of observed effect sizes should be compared against predicted variability and how the presence of bias influences the interpretation of a meta-analysis. Thus, he concludes that “even so [biases may exist], meta-analysis can give the best estimates justified by research to date, as well as the best guidance for practitioners” (p. 23). Thus, the new statistics would suggest that extrasensory perception is real because a meta-analysis of Bem’s (2011) infamous Journal of Personality and Social Psychology article shows an effect with a tight confidence interval that does not include zero. In contrast, other researchers have demonstrated with old statistical tools and with the help of post-hoc power that Bem’s results are not credible (Francis, 2012; Schimmack, 2012).

Research Integrity

Cumming also advocates research integrity. His first point is that psychological science should “promote research integrity: (a) a public research literature that is complete and trustworthy and (b) ethical practice, including full and accurate reporting of research” (p. 8). However, his own article falls short of this ideal. His article does not provide a complete, balanced, and objective account of the statistical literature. Rather, Cumming (2014) cheery-picks references that support his claims and does not cite references that are inconvenient for his claims. I give one clear example of bias in his literature review.

He cites Ioannidis’s 2005 paper to argue that p-values and NHST is flawed and should be abandoned. However, he does not cite Ioannidis and Trikalinos (2007). This article introduces a statistical approach that can detect biases in meta-analysis by comparing the success rate (percentage of significant results) to the observed power of the studies. As power determines the success rate in an honest set of studies, a higher success rate reveals publication bias. Cumming not only fails to mention this article. He goes on to warn readers “beware of any power statement that does not state an ES; do not use post hoc power.” Without further elaboration, this would imply that readers should ignore evidence for bias with the Test of Excessive Significance because it relies on post-hoc power. To support this claim, he cites Hoenig and Heisey (2001) to claim that “post hoc power can often take almost any value, so it is likely to be misleading” (p. 24). This statement is misleading because post-hoc power is no different from any other statistic that is influenced by sampling error. In fact,Hoenig and Heisey (2001) show that post-hoc power in a single study is monotonically related to p-values. Their main point is that post-hoc power provides no other information than p-values. However, like p-values, post-hoc power becomes more informative, the higher it is. A study with 99% post-hoc power is likely to be a high powered study, just like extremely low p-values, p < .0001, are unlikely to be obtained in low powered studies or in studies when the null-hypothesis is true. So, post-hoc power is informative when it is high. Cumming (2014) further ignores that variability of post-hoc power estimates decreases in a meta-analysis of post-hoc power and that post-hoc power has been used successfully to reveal bias in published articles (Francis, 2012; Schimmack (2012). Thus, his statement that researchers should ignore post-hoc power analyses is not supported by an unbiased review of the literature, and his article does not provide a complete and trustworthy account of the public research literature.

Conclusion

I cannot recommend Cumming’s new statistics. I routinely report confidence intervals in my empirical articles, but I do not consider them as a new statistical tool. In my opinion, the root cause of the credibility crisis is that researchers conduct underpowered studies that have a low chance to produce the predicted effect and then use questionable research practices to boost power and to hide non-significant results that could not be salvaged. A simple solution to this problem is to conduct more powerful studies that can produce significant results when the predict effect exists. I do not claim that this is a new insight. Rather, Jacob Cohen has tried his whole life to educate psychologists about the importance of statistical power.

Here is what Jacob Cohen had to say about the new statistics in 1994 using time-travel to comment on Cumming’s article 20 years later.

“Everyone knows” that confidence intervals contain all the information to be found in significance tests and much more. They not only reveal the status of the trivial nil hypothesis but also about the status of non-nil null hypotheses and thus help remind researchers about the possible operation of the crud factor. Yet they are rarely to be found in the literature. I suspect that the main reason they are not reported is that they are so embarrassingly large! But their sheer size should move us toward improving our measurement by seeking to reduce the unreliable and invalid part of the variance in our measures (as Student himself recommended almost a century ago). Also, their width provides us with the analogue of power analysis in significance testing—larger sample sizes reduce the size of confidence intervals as they increase the statistical power of NHST” (p. 1002).

If you are looking for a book on statistics, I recommend Cohen’s old statistics over Cumming’s new statistics, p < .05.

Conflict of Interest: I do not have a book to sell (yet), but I strongly believe that power analysis is an important tool for all scientists who have to deal with uncontrollable variance in their data. Therefore I am strongly opposed to Cumming’s push for a new statistics that provides no guidelines for researchers how they can optimize the use of their resources to obtain credible evidence for effects that actually exist and no guidelines how science can correct false positive results.