Some videos on the internet are so good that I’ve watched them twice. Below is a list of 10 of my favorite interviews and dialogues. Obviously this isn’t an endorsement of all the positions taken. I just think they are very well done and fun to watch. The last four are best watched on 1.4x speed.

Everywhere you look, people are optimizing bad metrics. Sometimes people optimize metrics that aren’t in their self interest, like when startups focus entirely on signup counts while forgetting about retention rates. In other cases, people optimize metrics that serve their immediate short term interest but which are bad for social welfare, like when California corrections officers lobby for longer prison sentences.

The good news is that as we become a more data-driven society, there seems to be a broad trend — albeit a very slow one — towards better metrics. Take the media economy, for example. A few years ago, media companies optimized for clicks, and companies like Upworthy thrived by producing low quality content with clickbaity headlines. But now, thanks to a more sustainable business model, companies like Buzzfeed are optimizing for shares rather than clicks. It’s not perfect, but overall it’s better for consumers.

In science, researchers used to optimize for publication counts and citation counts, which biased them towards publishing surprising and interesting results that were unlikely to be true. These metrics still loom large, but increasingly scientists are beginning to optimize for other metrics like open data badges and reproducibility, although we still have a long way to go before quality metrics are effectively measured and incentivized.

In health care, hospitals used to profit by maximizing the quantity of care. Perversely, hospitals benefited whenever patients were readmitted due to infections acquired in the hospital or due to lack of adequate follow-up plan. Now, with ACApolicies that penalize hospitals for avoidable readmissions, hospitals are taking real steps to improve follow-up care and to reduce hospital-acquired infections. While the metrics should beadjusted so that they don’t unfairly penalize low income hospitals, the overall emphasis on quality rather than quantity is moving things in the right direction.

We still are light years from where we need to be, and bad incentives continue to plague everything from government to finance to education. But slowly, as we get better at measuring and storing data, I think we are getting at picking the right metrics.

Like most people who have analyzed data using frequentist statistics, I have often found myself staring at error bars and trying to guess whether my results are significant. When comparing two independent sample means, this practice is confusing and difficult. The conventions that we use for testing differences between sample means are not aligned with the conventions we use for plotting error bars. As a result, it’s fair to say that there’s a lot of confusion about this issue.

Some people believe that two independent samples have significantly different means if and only if their standard error bars (68% confidence intervals for large samples) don’t overlap. This belief is incorrect. Two samples can have nonoverlapping standard error bars and still fail to reach statistical significance at . Other people believe that two means are significantly different if and only if their 95% confidence intervals overlap. This belief is also incorrect. For one sample t-tests, it is true that significance is reached when the 95% confidence interval crosses the test parameter . But for two-sample t-tests, which are more common in research, statistical significance can occur with overlapping 95% confidence intervals.

If neither the 68% confidence interval nor the 95% confidence interval tells us anything about statistical significance, what does? In most situations, the answer is the 83.4% confidence interval. This can be seen in the figure below, which shows two samples with a barely significant difference in means (p=.05). Only the 83.4% confidence intervals shown in the third panel are barely overlapping, reflecting the barely significant results.

To understand why, let’s start by defining the t-statistic for two independent samples:

where and are the means of the two samples, and and are their standard errors. By rearranging, we can see that significant results will be barely obtained () if the following condition holds:

where 1.96 is the large sample cutoff for significance. Assuming equal standard errors (more on this later), the equation simplifies to:

On a graph, the quantity is the distance between the means. If we want our error bars to just barely touch each other, we should set the length of the half-error bar to be exactly half of this, or:

This corresponds to an 83.4% confidence interval on the normal distribution. While this result assumes a large sample size, it remains quite useful for sample sizes as low as 20. The 83.4% confidence interval can also become slightly less useful when the samples have strongly different standard errors, which can stem from very unequal sample sizes or variances. If you really want a solution that generalizes to this situation, you can set your half-error bar on your first sample to:

and make the appropriate substitutions to compute the half-error bar in your second sample. However, this solution has the undesirable property that the error bar for one sample depends on the standard error of the other sample. For most purposes, it’s probably better to just plot the 83% confidence interval. If you are eyeballing data for a project that requires frequentist statistics, it is arguably more useful than plotting the standard error or the 95% confidence interval.

Update: Jeff Rouder helpfully points me to Tryon and Lewis (2008), which presents an error bar that generalizes both to unequal standard errors and small samples. Like the last equation presented above, it has the undesirable property that the size of the error bar around a particular sample depends on both samples. But on the plus side, it’s guaranteed to tell you about significance.

I often need to jump between different directories with very deep paths, like this:

While it only takes a handful of seconds to switch directories, the extra mental effort often derails my train of thought. Some solutions exist, but they all have their limitations. For example, pushd and popd don’t work well for directories you haven’t visited in a while. Aliases require you to manually add a new alias to your .bashrc every time you want to save a new directory.

I recently found a solution, inspired by this post from Jeroen Janssens, that works great and feels totally natural. All it takes is a one-time change to your .bashrc that will allow you to easily save directories and switch between them. To save a directory, just use the mark function:

To navigate to a saved directory, just use the cdd function:

You can display a list of your saved directories with the marks function, and you can remove a directory from the list with the unmark function:

For any of this to work, you’ll need to add this to your .bashrc, assuming you have a Mac and use the bash shell.

This differs from Jeroen’s original code in a couple of ways. First, to be more brain-friendly, it names the function “cdd” instead of “jump”. Second, the tab completion works better.

Yesterday I posted a very unscientific survey asking researchers to describe how failed replications changed their subjective estimates of effect sizes. The main survey asked for “ballpark estimates” of effect sizes, but an alternative interactive version allowed researchers to also report their uncertainty by specifying both the mean and variance of their posterior distributions. Thanks to everyone who participated. I won’t be analyzing any new data after this, but it’s never too late to publicly share your estimates!

Here are the questions.

Question 1. A 2009 experiment with 50 subjects (25 per cell) is published in Psych Science. The experiment does not require any special equipment other than a questionnaire. It is not pre-registered. The results show an effect size of d=0.5. Let’s define the true effect size to be the average effect size of an infinite number of replications that the original experimenter would deem “reasonably exact” in advance. Based on this information alone, what is your ballpark subjective estimate of the true effect size?

Question 2. What if the experiment had been pre-registered?

Question 3. Assume again that the experiment was not pre-registered. Now imagine that a pre-registered replication attempt with the same sample size estimated the effect size to be d=0.0. At the time of pre-registration, the original experimenter deemed it “reasonably exact”. Based on this replication and the original experiment, what is your ballpark subjective estimate of the true effect size?

Question 4. What if the replication attempt had 300 subjects per cell?

Here are the results.

Keeping in mind all the caveats about sampling bias and other issues, here are a few observations:

The original study reported an effect size of d=0.5, but the results for Question 1 tell us that most researchers believed the true effect size was closer to d=0.2, which is roughly in line with my own estimate. Had I allowed researchers to state their uncertainty, I suspect that many would find it quite possible that even the sign of the effect was wrong. This isn’t really surprising to me, but I think we should take a moment to reflect on what this means. When a scientist reports a result, most other researchers believe it is massively overstated. I know that there are still some researchers who want little or no changes to the status quo, but I’d like to live in a world where people actually believe the claims that scientists make. That’s why I’m a strong supporter of all the attempts to fundamentallychangehow scientists do research.

If you want people to have more confidence in your findings, pre-registration can make a big difference.

While it’s not apparent from the plot, almost all respondents reduced their effect size estimate upon hearing about failed replications (Question 3 and 4 compared to Question 1).

As some have pointed out, the original experiment falls a bit short of statistical significance. This was an oversight, as I forgot to check the p-value after changing some of the values. I don’t think this is a huge deal, since posterior estimates shouldn’t really depend too much on whether the results cross an arbitrary threshold. But apologies for the error.