Replication is impossible, falsification unnecessary and truth lies in published articles (?)

Writing this piece crammed in the backseat of a car, because I’m a zealot (also, because I wanted to have a picture here).

I recently peer reviewed a partly shocking piece called “Reproducibility in Psychological Science: When Do Psychological Phenomena Exist?“ (Iso-Ahola, 2017). In the article, the author makes some very good points, which unfortunately get drowned under very strange statements and positions. Me, Eiko Fried and Etienne LeBel addressed those shortly in a commentary (preprint; UPDATE: published piece). Below, I’d like to expand upon some additional thoughts I had about the piece, to answer Martin Hagger’s question.

On complexity

When all parts do the same thing on a certain scale (planets on Newtonian orbits), their behaviour is relatively easy to predict for many purposes. Same thing, when all molecules act independently in a random fashion: the risk that most or all beer molecules in a pint move upward at the same time is ridiculously low, and thus we don’t have to worry about the yellow (or black, if you’re into that) gold escaping the glass. Both situations are easy-ish systems to describe, as opposed to complex systems where the interactions, sensitivity to initial conditions etc. can produce a huge variety of behaviour and states. Complexity science is the study of these phenomena, which have become increasingly common since the 1900s (Weaver, 1948).

Iso-Ahola (2017) quotes (though somewhat unfaithfully) the complexity scientist Bar-Yam (2016b): “for complex systems (humans), all empirical inferences are false… by their assumptions of replicability of conditions, independence of different causal factors, and transfer to different conditions of prior observations”. He takes this to mean that “phenomena’s existence should not be defined by any index of reproducibility of findings” and that “falsifiability and replication are of secondary importance to advancement of scientific fields”. But this is a highly misleading representation of the complexity science perspective.

In Bar-Yam’s article, he used an information theoretic approach to analyse the limits of what we can say about complex systems. The position is that while full description of systems via empirical observation is impossible, we should aim to identify the factors which are meaningful in terms of replicability of findings, or the utility of the acquired knowledge. As he elaborates elsewhere: “There is no utility to information that is only true in a particular instance. Thus, all of scientific inquiry should be understood as an inquiry into universality—the determination of the degree to which information is general or specific” (Bar-Yam, 2016a, p. 19).

This is fully in line with the Fisher quote presented in Mayo’s slides:

Fisher quote Mayo

The same goes for replications; no single one-lab study can disprove a finding:

“’Thus a few stray basic statements contradicting a theory will hardly induce us to reject it as falsified. We shall take it as falsified only if we discover a reproducible effect which refutes the theory. In other words, we only accept the falsification if a low-level empirical hypothesis which describes such an effect is proposed and  corroborated’ (Popper, 1959, p. 66)” (see Holtz & Monnerjahn, 2017)

So, if the high-quality non-replication replicates, one must consider that something may be off with the original finding. This leads us to the question of what researchers should study in the first place.

On research programmes

Lakatos (1971) posits a difference between progressive and degenerating research lines. In a progressive research line, investigators explain a negative result by modifying the theory in a way which leads to new predictions that subsequently pan out. On the other hand, coming up with explanations that do not make further contributions, but rather just explain away the negative finding, leads to a degenerative research line. Iso-Ahola quotes Lakatos to argue that, although theories may have a “poor public record” that should not be denied, falsification should not lead to abandonment of theories. Here’s Lakatos:

“One may rationally stick to a degenerating [research] programme until it is overtaken by a rival and even after. What one must not do is to deny its poor public record. […] It is perfectly rational to play a risky game: what is irrational is to deceive oneself about the risk” (Lakatos, 1971, p. 104)

As Meehl (1990, p. 115) points out, the quote continues as follows:

“This does not mean as much licence as might appear for those who stick to a degenerating programme. For they can do this mostly only in private. Editors of scientific journals should refuse to publish their papers which will, in general, contain either solemn reassertions of their position or absorption of counterevidence (or even of rival programmes) by ad hoc, linguistic adjustments. Research foundations, too, should refuse money.” (Lakatos, 1971, p. 105)

Perhaps researchers should pay more attention which program they are following?

As an ending note, here’s one more interesting quote: “Zealotry of reproducibility has unfortunately reached the point where some researchers take a radical position that the original results mean nothing if not replicated in the new data.” (Iso-Ahola, 2017)

For explorative research, I largely agree with these zealots. I believe exploration is fine and well, but the results do mean nearly nothing unless replicated in new data (de Groot, 2014). One cannot hypothesise and confirm with the same data.

Perhaps I focus too much on the things that were said in the paper, not what the author actually meant, and we do apologise if we have failed to abide with the principle of charity in the commentary or this blog post. In a later post, I will attempt to show how the ten criteria Iso-Ahola proposed could be used to evaluate research.

ps. If you’re interested in replication matters in health psychology, there’s an upcoming symposium on the topic in EHPS17 featuring Martin Hagger, Gjalt-Jorn Peters, Rik Crutzen, Marie Johnston and me. My presentation is titled “Disentangling replicable mechanisms of complex interventions: What to expect and how to avoid fooling ourselves?


Bar-Yam, Y. (2016a). From big data to important information. Complexity, 21(S2), 73–98.

Bar-Yam, Y. (2016b). The limits of phenomenology: From behaviorism to drug testing and engineering design. Complexity, 21(S1), 181–189.

de Groot, A. D. (2014). The meaning of “significance” for different types of research [translated and annotated by Eric-Jan Wagenmakers, Denny Borsboom, Josine Verhagen, Rogier Kievit, Marjan Bakker, Angelique Cramer, Dora Matzke, Don Mellenbergh, and Han L. J. van der Maas]. Acta Psychologica, 148, 188–194.

Holtz, P., & Monnerjahn, P. (2017). Falsificationism is not just ‘potential’ falsifiability, but requires ‘actual’ falsification: Social psychology, critical rationalism, and progress in science. Journal for the Theory of Social Behaviour.

Iso-Ahola, S. E. (2017). Reproducibility in Psychological Science: When Do Psychological Phenomena Exist? Frontiers in Psychology, 8.

Lakatos, I. (1971). History of science and its rational reconstructions. Springer. Retrieved from

Meehl, P. E. (1990). Appraising and amending theories: The strategy of Lakatosian defense and two principles that warrant it. Psychological Inquiry, 1(2), 108–141.

Weaver, W. (1948). Science and complexity. American Scientist, 36(4), 536–544.


The art of expecting p-values

In this post, I try to present the intuition behind the fact that, when studying real effects, one usually should not expect p-values near the 0.05 threshold. If you don’t read quantitative research, you may want to skip this one. If you think I’m wrong about something, please leave a comment and set the record straight!

Recently, I attended a presentation by a visiting senior scholar. He spoke about how their group had discovered a surprising but welcome correlation between two measures, and subsequently managed to replicate the result. What struck me, was his choice of words:

“We found this association, which was barely significant. So we replicated it with the same sample size of ~250, and found that the correlation was almost the same as before and, as expected, of similar statistical significance (p < 0.05)“.

This highlights a threefold, often implicit (but WRONG), mental model:

[EDIT: due to Markus’ comments, I realised the original, off-the-top-of-my-head examples were numerically impossible and changed them a bit. Also, added stuff in brackets that the post hopefully clarifies as you read on.]

  1. “Replications with a sample size similar to the original, should produce p-values similar to the original.”
    • Example: in subsequent studies with n = 100 each, a correlation (p = 0.04) should replicate as the same correlation (p ≈ 0.04) [this happens about 0.02% of the time when population r is 0.3; in these cases you actually observe an r≈0.19]
  2. “P-values are linearly related with sample size, i.e. bigger sample gives you proportionately more small p-values.”
    • Example: a correlation (n = 100, p = 0.04), should replicate as a correlation of about the same, when n = 400, with e.g. a p ≈ 0.02. [in the above-mentioned case, the replication gives observed r±0.05 about 2% of the time, but the p-value is smaller than 0.0001 for the replication]
  3. “We study real effects.” [we should think a lot more about how our observations could have come by in the absence of a real effect!]

It is obvious that the third point is contentious, and I won’t consider it here much. But the first two points are less clear, although the confusion is understandable if one has learned and always applied Jurassic (pre-Bem) statistics.

[Note: “statistical power” or simply “power” is the probability of finding an effect, if it really exists. The more obvious an effect is, and the bigger your sample size, the better are your chances of detecting these real effects – i.e. you have bigger power. You want to be pretty sure your study detects what it’s designed to detect, so you may want to have a power of 90%, for example.]

Figure 1. A lottery machine. Source: Wikipedia

To get a handle of how the p behaves, we must understand the nature of p-values as random variables 1. They are much like the balls in a lottery machine, with values between zero and one marked on them. The lottery machine of real effects has disproportionately more low (e.g. < 0.01) values on the balls, while the lottery machine of null effects contains a “fair” distribution of numbers on balls (where each number is as likely as any other). If this doesn’t make sense yet, read on.

Let us exemplify this with a simulation. Figure 2 shows the expected distribution of p-values, when we do 10 000 studies with one t-test each, and every time report the p of the test. You can think of this as 9999 replications with the same sample size as the original.

Figure 2: p-value distribution for 10 000 simulated studies, under 50% power when the alternative hypothesis is true. (When power increases, the curve gets pushed even farther to the left, leaving next to no p-values over 0.01)

Now, if we would do just five studies with the parameters laid out above, we could see a set of p-values like {0.002, 0.009, 0.024, 0.057, 0.329, 0.479}, half of them being “significant” (in bold). If we had 80% power to detect the difference we are looking for, about 80% of the p-values would be “significant”. As an additional note, with 50% power, 4% of the 10 000 studies give a p between 0.04 and 0.05. With 80% power, this number goes down to 3%. For 97.5% power, only 0.5%  of studies (yes, five for every thousand studies) are expected to give such a “barely significant” p-value.

The senior scholar, who was mentioned in the beginning, was studying correlations. They work the same way. The animation below shows, how p-values are distributed for different sample sizes, if we do 10 000 studies with every sample size (i.e. every frame is 10 000 studies with that sample size). The samples are from a population where the real correlation is 0.3. The red dotted line is p = 0.05.

Figure 3. P-value distributions for different sample sizes, when studying a real correlation of 0.3. Each frame is 10 000 replications with a given sample size. If pic doesn’t show, click here for the gif (and/or try another browser).

The next animation zooms in on “significant” p-values in the same way as in figure 2 (though the largest bar goes off the roof quickly here). As you can see, it is almost impossible to get a p-value close to 5% with large power. Thus, there is no way we should “expect” a p-value over 0.01 when we replicate a real effect with large power. Very low p-values are always more probable than “barely significant” ones.

Figure 4. Zooming in on the “significant” p-values. It is more probable to get a very low p than a barely significant one, even with small samples. If pic doesn’t show, click here for the gif.

But what if there is no effect? In this case, every p-value is equally likely (see Figure 5). This means, that in the long run, getting a p = 0.01 is just as likely as getting a p = 0.97, and by implication, 5% of all p-values are under 0.05. Therefore, the number of studies that generated a p between 0.04 and 0.05, is 1%. Remember, how this percentage was 0.5% (five in a thousand) when the alternative hypothesis was true under 97.5% power? Indeed, when power is high, these “barely significant” p-values may actually speak for the null, not the alternative hypothesis! Same goes for e.g. p=0.024, when power is 99% [see here].

Figure 5. p-value distribution when the null hypothesis is true. Every p is just as likely as any other.

Consider the lottery machine analogy again. Does it make better sense now?

The lottery machine of real effects has disproportionately more low (e.g. < 0.01) values on the balls, while the lottery machine of null effects contains a “fair” distribution of numbers on balls (each number is as likely as any other).

Let’s look at one more visualisation of the same thing:

Figure 6. The percentages of “statistically significant” p-values evolving as sample size increases. If the gif doesn’t show, you’ll find it here.

Aside: when the effect one studies is enormous, sample size naturally matters less. I calculated Cohen’s d for the Asch 2 line segment study, and a whopping d = 1.59 emerged. This is surely a very unusual effect size in psychological experiments, and leads to high statistical power even under low sample sizes. In such a case, by the logic presented above, one should be extremely cautious of p-values closer to 0.05 than zero.

Understanding all this is vital in interpreting past research. We never know what the data generating system has been (i.e. are p-values extracted from a distribution under the null, or under the alternative), but the data gives us hints about what is more likely. Let us take an example from a social psychology classic, Moscovici’s “Towards a theory of conversion behaviour” 3. The article reviews results, which are then used to support a nuanced theory of minority influence. Low p-values are taken as evidence for an effect.

Based on what we learned earlier about the distribution of p-values under the null vs. the alternative, we can now see, under which hypothesis the p-values are more likely to occur. The tool to use here is called the p-curve 4, and it is presented in Figure 6.

Figure 6. A quick-and-dirty p-curve of Moscovici (1980). See this link for the data you can paste onto p-checker or p-curve.

You can directly see, how a big portion of p-values is in the 0.05 region, whereas you would expect them to cluster near 0.01. The p-curve analysis (from the p-curve website) shows that evidential value, if there is any, is inadequate (Z = -2.04, p = .0208). Power is estimated to be 5%, consistent with the null hypothesis being true.

The null being true may or may not have been the case here. But looking at the curve might have helped researchers, who spent some forty years trying to unsuccessfully replicate the pattern of Moscovici’s afterimage study results 5.

In a recent talk, I joked about a bunch of researchers who tour around holiday resorts every summer, making people fill in IQ tests. Each summer they keep the results which show p < 0.05 and scrap the others, eventually ending up in the headlines with a nice meta-analysis of the results.

Don’t be those guys.


Disclaimer: the results discussed here may not generalise to some more complex models, where the p-value is not uniformly distributed under the null. I don’t know much about those cases, so please feel free to educate me!

Code for the animated plots is here. It was inspired by code from Daniel Lakens, whose blog post inspired this piece. Check out his MOOC here. Additional thanks to Jim Grange for advice on gif making and Alexander Etz for constructive comments.


  1. Murdoch, D. J., Tsai, Y.-L. & Adcock, J. P-Values are Random Variables. The American Statistician 62, 242–245 (2008).
  2. Asch, S. E. Studies of independence and conformity: I. A minority of one against a unanimous majority. Psychological monographs: General and applied 70, 1 (1956).
  3. Moscovici, S. in Advances in Experimental Social Psychology 13, 209–239 (Elsevier, 1980).
  4. Simonsohn, U., Simmons, J. P. & Nelson, L. D. Better P-curves: Making P-curve analysis more robust to errors, fraud, and ambitious P-hacking, a Reply to Ulrich and Miller (2015). J Exp Psychol Gen 144, 1146–1152 (2015).
  5. Smith, J. R. & Haslam, S. A. Social psychology: Revisiting the classic studies. (SAGE Publications, 2012).

How lack of transparency feeds the beast

This is a presentation I held for the young researchers branch of the Finnish Psychological Society. I show how low power and lack of transparency can lead to weird situations, where the published literature contains little or no knowledge.


We had big fun with Markus Mattsson and Leo Aarnio in a seminar, presenting to a great audience of eager young researchers.

The slides for my talk are here:

If you’re interested in more history and solutions, check out Felix Schönbrodt‘s slides here. Some pictures were made adapting code from a wonderful Coursera MOOC by Daniel Lakens. For Bayes, check out Alexander Etz‘s blog.

Oh, and for the monster analogy; this piece made me think of it.

Getting Started With Bayes

This post presents a Bayesian roundtable I convened for the EHPS/DHP 2016 health psychology conference. Slides for the three talks are included.

bayes healthpsych cover

So, we kicked off the session with Susan Michie and acknowledged Jamie Brown who was key in making it happen, but could not attend.


Robert West was the first to present, you’ll find his slides “Bayesian analysis: a brief introductionhere. This presentation gave a brief introduction to Bayes and how belief updating with Bayes Factors works.

I was the second speaker, building on Robert’s presentation. Here are slides for my talk, where I introduced some practical resources to get started with Bayes. The slides are also embedded below (some slides got corrupted by Slideshare, so the ones in the .ppt link are a bit nicer).

The third and final presentation was by Niall Bolger. In his talk, he gave a great example of how using Bayes in a multilevel model enabled him to incorporate more realistic assumptions and—consequently—evaporate a finding he had considered somewhat solid. His slides, “Bayesian Estimation: Implications for Modeling Intensive Longitudinal Data“, are here.

Let me know if you don’t agree with something (especially in my presentation) or have ideas regarding how to improve the methods in (especially health) psychology research!