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Sisällysluettelon löydät oikeanpuoleisesta palkista.

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# Data punk | Käyttäytymisarkkitehtuuri

## Health psychology, scientific methodology and living with uncertainty

# Welcome / Tervetuloa!

# Missing data, the inferential assassin

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

## On complexity

## On research programmes

# Evaluating intervention program theories – as theories

# Preprints, short and sweet

# Death doesn’t kill you (and other reasons to study behaviour change)

# Deterministic doesn’t mean predictable

# What are the consequences?

# The art of expecting p-values

Check out categories and post index on the right hand panel.

Sisällysluettelon löydät oikeanpuoleisesta palkista.

Last week, I attended the Methods festival 2017 in Jyväskylä. Slides and program for the first day are here, and for the second day, here (some are in Finnish, some in English).

One interesting presentation was on missing data by Juha Karvanen [twitter profile] (slides for the talk). It involved toilet paper and Hans Rosling, so I figured I’ll post my recording of the display. Thing is, missing data lurks in the shadows and if you don’t do your utmost to get full information, *it may be lethal*.

- Intro and missing completely at random (MCAR): Video. Probability of missingness for all cases is the same. Rare in real life?
- Missing at random (MAR): Video. Probability of missingness depends on something we know. For example, if men leave more questions unanswered than women, but among men and women, the missingness is MCAR.
- Missing not at random (MNAR): Video. Probability of missingness depends on unobserved values. Your analysis becomes misleading and you may not know it; misinformation reigns and angels cry.

There was an exciting question on a slide. I’ll post the answer in this thread later.

By the way, one of Richard McElreath’s Statistical Rethinking lectures has a nice description on how to do Bayesian imputation when one assumes MCAR. He also discusses of how irrational complete case analysis (throwing away the cases that don’t have full data) is, when you really think about it. Also, **never substitute a missing value with the mean of other values!**

p.s. I would love it if someone dropped a comment saying “this problem is actually not too dire, because…”

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.

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:

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.

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?*“

Bibliography:

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. https://doi.org/10.1002/cplx.21730

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. https://doi.org/10.1016/j.actpsy.2014.02.001

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*. https://doi.org/10.1111/jtsb.12134

Iso-Ahola, S. E. (2017). Reproducibility in Psychological Science: When Do Psychological Phenomena Exist? *Frontiers in Psychology*, *8*. https://doi.org/10.3389/fpsyg.2017.00879

Lakatos, I. (1971). *History of science and its rational reconstructions*. Springer. Retrieved from http://link.springer.com/chapter/10.1007/978-94-010-3142-4_7

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.

*How do we figure out, whether our ideas worked out? These are slides for my talk — Tuesday 2nd May — at the Finnish National Institute for Health and Welfare (THL).* *Would love to get feedback, if you have proposals to solve the problems presented! You can download a pdf here.*

TLDR: is there a reason, why evaluating intervention program theories shouldn’t follow the process of scientific inference?

*These are slides (with added text content to make more sense) from a small presentation I held at the University of Helsinki. Mainly of interest to academic researchers. *

TL;DR: To get the most out of scientific publishing, we may need imitate physics a bit, and bypass the old gatekeepers. If the slideshare below is of crappy quality, check out the slides here.

ps. if you prefer video, this explains things in four minutes 🙂

*This is a talk I gave to a group of master’s students in social psychology. It introduces the crisis of confidence in science, how non-communicable diseases can be thought of as symptom networks, and some basics of behaviour change research.*

*In this post, I argue against the intuitively appealing notion that, in a deterministic world, we just need more information and can use it to solve problems in complex systems. This presents a problem in e.g. psychology, where more knowledge does not necessarily mean cumulative knowledge or even improved outcomes.*

Recently, I attended a talk where Misha Pavel happened to mention how big data can lead us astray, and how we can’t just look at data but need to know mechanisms of behaviour, too.

Later, a couple of my psychologist friends happened to present arguments discounting this, saying that the problem will be solved due to determinism. Their idea was that the world is a deterministic place—if we knew everything, we could predict everything (an argument also known as Laplace’s Demon)—and that we eventually a) will know, and b) can predict. I’m fine with the first part, or at least agnostic about it. But there are more mundane problems to prediction than “quantum randomness” and other considerations about whether truly random phenomenon exist. The thing is, that *even simple and completely deterministic systems can be utterly unpredictable *to us mortals. I will give an example of this below.

Even simple and completely deterministic systems can be utterly unpredictable.

Let’s think of a very simple made-up model of physical activity, just to illustrate a phenomenon:

Say today’s amount of exercise depends only on motivation and exercise of the previous day. Let’s say people have a certain maximum amount of time to exercise each day, and that they vary from day to day, in what proportion of that time they actually manage to exercise. To keep things simple, let’s say that if a person manages to do more exercise on Monday, they give themselves a break on Tuesday. People also have different motivation, so let’s add that as factor, too.

Our completely deterministic, but definitely wrong, model could generalise to:

Exercise percentage today = (motivation) * (percentage of max exercise yesterday) * (1 – percentage of max exercise yesterday)

For example, if one had a constant motivation of 3.9 units (whatever the scale), and managed to do 80% of their maximum exercise on Monday, they would use 3.9 times 80% times 20% = 62% of their maximum exercise time on Tuesday. Likewise, on Wednesday they would use 3.9 times 62% times 38% = 92% of the maximum possible exercise time. And so on and so on.

We’re pretending this model is *the* reality. This is so that we can perfectly calculate the amount of exercise on any day, given that we know a person’s motivation and how much they managed to exercise the previous day.

Imagine we measure a person, who obeys this model with a constant motivation of 3.9, and starts out on day 1 reaching 50% of their maximum exercise amount. But let’s say there is a slight measurement error: instead of 50.000%, we measure 50.001%. In the graph below we can observe, how the error (red line) quickly diverges from the actual (blue line). The predictions we make from our model after around day 40 do not describe our target person’s behaviour at all. The slight deviation from the deterministic system has made it practically chaotic and random to us.

The model is silly, of course, as we probably would never try to predict an individual’s exact behaviour on any single day (averages and/or bigger groups help, because usually no single instance can kill the prediction). But this example does highlight a common feature of complex systems, known as *sensitive dependence to initial conditions: *even small uncertainties cumulate to create huge errors. It is also worth noting, that increasing model complexity doesn’t necessarily help us with prediction, due to a problems such as overfitting (thinking the future will be like the past; see also why simple heuristics can beat optimisation).

Thus, predicting long-term path-dependent behaviour, even if we knew the exact psycho-socio-biological mechanism governing it, may be impossible in the absence of *perfect* measurement. Even if the world was completely deterministic, we still could not predict it, as even trivially small things left unaccounted for could throw us off completely.

Predicting

long-term path-dependent behaviour, even if we knew the exact psycho-socio-biological mechanism governing it, may be impossible in the absence ofmeasurement.perfect

The same thing happens when trying to predict as simple a thing as how billiard balls impact each other on the pool table. The first collision is easy to calculate, but to compute the ninth you already have to take into account the gravitational pull of people standing around the table. By the 56th impact, every elementary particle in the universe has to be included in your assumptions! Other examples include trying to predict the sex of a human fetus, or trying to predict the weather 2 weeks out (this is the famous idea about the butterfly flapping its wings).

Coming back to Misha Pavel’s points regarding big data, I feel somewhat skeptical about being able to acquire invariant “domain knowledge” in many psychological domains. Also, as shown here, knowing the exact mechanism is still no promise of being able to predict what happens in a system. Perhaps we should be satisfied when we can make predictions such as “intervention x will increase the probability that the system reaches a state where more than 60% of the goal is reached on more than 50% of the days, by more than 20% in more than 60% of the people who belong in a group it was designed to affect”?

But still: for determinism to solve our prediction problems, the amount and accuracy of data needed is beyond the wildest sci-fi fantasies.

I’m happy to be wrong about this, so please share your thoughts! Leave a comment below, or on these relevant threads: Twitter, Facebook.

References and resources:

- Code for the plot can be found here.
- The billiard ball example explained in context.
- A short paper on the history about the butterfly (or seagull) flapping its wings-thing.
- To learn about dynamic systems and chaos, I highly recommend David Feldman’s course on the topic, next time it comes around at Complexity Explorer.
- … Meanwhile, the equation I used here is actually known as the “logistic map”. See this post about how it behaves.

*Post scriptum:*

Recently, I was happy and surprised to see a paper attempting to create a computational model of a major psychological theory. In a conversation, Nick Brown expressed doubt:

Do you agree? What are the alternatives? Do we have to content with vague statements like “the behaviour will fluctuate”* (*perhaps as in:* fluctuat nec mergitur)*? How should we study the dynamics of human behaviour?

Also: do see Nick Brown’s blog, if you don’t mind non-conformist thinking.

*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.]

- “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]

- “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]

- “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.]

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.

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.

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.

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].

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:

*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 un**der 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.

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.

**Bibliography:**

- Murdoch, D. J., Tsai, Y.-L. & Adcock, J. P-Values are Random Variables.
*The American Statistician***62,**242–245 (2008). - 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). - Moscovici, S. in
*Advances in Experimental Social Psychology***13,**209–239 (Elsevier, 1980). - 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). - Smith, J. R. & Haslam, S. A.
*Social psychology: Revisiting the classic studies*. (SAGE Publications, 2012).