# What is the Bayesian justification for privileging analyses conducted earlier than other analyses?

### Background and Empirical Example

I have two studies; I ran an experiment (Study 1) and then replicated it (Study 2). In Study 1, I found an interaction between two variables; in Study 2, this interaction was in the same direction but not significant. Here is the summary for Study 1's model:

Coefficients:
Estimate Std. Error t value Pr(>|t|)
(Intercept)              5.75882    0.26368  21.840  < 2e-16 ***
condSuppression         -1.69598    0.34549  -4.909 1.94e-06 ***
prej                    -0.01981    0.08474  -0.234  0.81542
condSuppression:prej     0.36342    0.11513   3.157  0.00185 **


And Study 2's model:

Coefficients:
Estimate Std. Error t value Pr(>|t|)
(Intercept)           5.24493    0.24459  21.444   <2e-16 ***
prej                  0.13817    0.07984   1.731   0.0851 .
condSuppression      -0.59510    0.34168  -1.742   0.0831 .
prej:condSuppression  0.13588    0.11889   1.143   0.2545


Instead of saying, "I guess I don't have anything, because I 'failed to replicate,'" what I did was combine the two data sets, created a dummy variable for what study the data came from, and then ran the interaction again after controlling for study dummy variable. This interaction was significant even after controlling for it, and I found that this two-way interaction between condition and dislike/prej was not qualified by a three-way interaction with the study dummy variable.

### Introducing Bayesian Analysis

I had someone suggest that this is a great opportunity to use Bayesian analysis: In Study 2, I have information from Study 1 that I can use as prior information! In this way, Study 2 is doing a Bayesian updating from the frequentist, ordinary least squares results in Study 1. So, I go back and re-analyze the Study 2 model, now using informative priors on the coefficients: All the coefficients had a normal prior where the mean was the estimate in Study 1 and the standard deviation was the standard error in Study 1.

This is a summary of the result:

Estimates:
mean    sd      2.5%    25%     50%     75%     97.5%
(Intercept)             5.63    0.17    5.30    5.52    5.63    5.74    5.96
condSuppression        -1.20    0.20   -1.60   -1.34   -1.21   -1.07   -0.80
prej                    0.02    0.05   -0.08   -0.01    0.02    0.05    0.11
condSuppression:prej    0.34    0.06    0.21    0.30    0.34    0.38    0.46
sigma                   1.14    0.06    1.03    1.10    1.13    1.17    1.26
mean_PPD                5.49    0.11    5.27    5.41    5.49    5.56    5.72
log-posterior        -316.40    1.63 -320.25 -317.25 -316.03 -315.23 -314.29


It looks like now we have pretty solid evidence for an interaction from the Study 2 analysis. This agrees with what I did when I simply stacked the data on top of one another and ran the model with study number as a dummy-variable.

### Counterfactual: What If I Ran Study 2 First?

That got me thinking: What if I had run Study 2 first and then used the data from Study 1 to update my beliefs on Study 2? I did the same thing as above, but in reverse: I re-analyzed the Study 1 data using the frequentist, ordinary least squares coefficient estimates and standard deviations from Study 2 as prior means and standard deviations for my analysis of Study 1 data. The summary results were:

Estimates:
mean    sd      2.5%    25%     50%     75%     97.5%
(Intercept)                5.35    0.17    5.01    5.23    5.35    5.46    5.69
condSuppression           -1.09    0.20   -1.47   -1.22   -1.09   -0.96   -0.69
prej                       0.11    0.05    0.01    0.08    0.11    0.14    0.21
condSuppression:prej       0.17    0.06    0.05    0.13    0.17    0.21    0.28
sigma                      1.10    0.06    0.99    1.06    1.09    1.13    1.21
mean_PPD                   5.33    0.11    5.11    5.25    5.33    5.40    5.54
log-posterior           -303.89    1.61 -307.96 -304.67 -303.53 -302.74 -301.83


Again, we see evidence for an interaction, however this might not have necessarily been the case. Note that the point estimate for both Bayesian analyses aren't even in the 95% credible intervals for one another; the two credible intervals from the Bayesian analyses have more non-overlap than they do overlap.

### What Is The Bayesian Justification For Time Precedence?

My question is thus: What is the justifications that Bayesians have for respecting the chronology of how the data were collected and analyzed? I get results from Study 1 and use them as informative priors in Study 2 so that I use Study 2 to "update" my beliefs. But if we assume that the results I get are randomly taken from a distribution with a true population effect... then why do I privilege the results from Study 1? What is the justification for using Study 1 results as priors for Study 2 instead of taking Study 2 results as priors for Study 1? Does the order in which I collected and calculated the analyses really matter? It does not seem like it should to me—what is the Bayesian justification for this? Why should I believe the point estimate is closer to .34 than it is to .17 just because I ran Study 1 first?

Kodiologist remarked:

The second of these points to an important departure you have made from Bayesian convention. You didn't set a prior first and then fit both models in Bayesian fashion. You fit one model in a non-Bayesian fashion and then used that for priors for the other model. If you used the conventional approach, you wouldn't see the dependence on order that you saw here.

To address this, I fit the models for Study 1 and Study 2 where all regression coefficients had a prior of $\text{N}(0, 5)$. The cond variable was a dummy variable for experimental condition, coded 0 or 1; the prej variable, as well as the outcome, were both measured on 7-point scales ranging from 1 to 7. Thus, I think it is a fair choice of prior. Just by how the data are scaled, it would be very, very rare to see coefficients much larger than what that prior suggests.

The mean estimates and standard deviation of those estimates are about the same as in the OLS regression. Study 1:

Estimates:
mean     sd       2.5%     25%      50%      75%      97.5%
(Intercept)             5.756    0.270    5.236    5.573    5.751    5.940    6.289
condSuppression        -1.694    0.357   -2.403   -1.925   -1.688   -1.452   -0.986
prej                   -0.019    0.087   -0.191   -0.079   -0.017    0.040    0.150
condSuppression:prej    0.363    0.119    0.132    0.282    0.360    0.442    0.601
sigma                   1.091    0.057    0.987    1.054    1.088    1.126    1.213
mean_PPD                5.332    0.108    5.121    5.259    5.332    5.406    5.542
log-posterior        -304.764    1.589 -308.532 -305.551 -304.463 -303.595 -302.625


And Study 2:

Estimates:
mean     sd       2.5%     25%      50%      75%      97.5%
(Intercept)             5.249    0.243    4.783    5.082    5.246    5.417    5.715
condSuppression        -0.599    0.342   -1.272   -0.823   -0.599   -0.374    0.098
prej                    0.137    0.079   -0.021    0.084    0.138    0.192    0.287
condSuppression:prej    0.135    0.120   -0.099    0.055    0.136    0.214    0.366
sigma                   1.132    0.056    1.034    1.092    1.128    1.169    1.253
mean_PPD                5.470    0.114    5.248    5.392    5.471    5.548    5.687
log-posterior        -316.699    1.583 -320.626 -317.454 -316.342 -315.561 -314.651


Since these means and standard deviations are the more or less the same as the OLS estimates, the order effect above still occurs. If I plug-in the posterior summary statistics from Study 1 into the priors when analyzing Study 2, I observe a different final posterior than when analyzing Study 2 first and then using those posterior summary statistics as priors for analyzing Study 1.

Even when I use the Bayesian means and standard deviations for the regression coefficients as priors instead of the frequentist estimates, I would still observe the same order effect. So the question remains: What is the Bayesian justification for privileging the study that came first?

• "I would still be in the same situation. So the question remains: What is the Bayesian justification for privileging the study that came first?" — Huh? In what sense are you still privileging Study 1? You can fit the two models as you described here or in the opposite order and your final estimate of e.g. the true population coefficient for prej should be the same either way, unless I'm misunderstanding your procedure. Apr 28, 2018 at 6:58
• @Kodiologist I edited for clarity, including more about the procedure. Apr 28, 2018 at 13:26
• What about the the covariance matrix & the error? You've got to use the whole joint posterior as your new prior. Apr 28, 2018 at 13:26
• @Scortchi bingo—that is the correct answer, I think, and it was what unutbu's answer led me to believe. What I did was a really crude version of updating: I took summary statistics, not the entire joint posterior. That implies the question: Is there a way to include the whole joint posterior as a prior in rstanarm or Stan? It seems like that question has been asked here before: stats.stackexchange.com/questions/241690/… Apr 28, 2018 at 13:29
• If you're starting with Gaussian priors (& independence?) for the coefficients & an inverse-gamma for the variance, then you've got a normal inverse-gamma prior & it's conjugate. Look up the updating equations. Apr 28, 2018 at 13:33

Bayes' theorem says the posterior is equal to prior * likelihood after rescaling (so the probability sums to 1). Each observation has a likelihood which can be used to update the prior and create a new posterior:

posterior_1 = prior * likelihood_1
posterior_2 = posterior_1 * likelihood_2
...
posterior_n = posterior_{n-1} * likelihood_n


So that

posterior_n = prior * likelihood_1 * ... * likelihood_n


The commutativity of multiplication implies the updates can be done in any order. So if you start with a single prior, you can mix the observations from Study 1 and Study 2 in any order, apply Bayes' formula and arrive at the same final posterior.

• Makes perfect sense. So this points to a possible reason for the discrepancy as being: the way I did my analyses (plug posterior summary statistics into the prior arguments for the next study) is not how updating works? That is: I need to consider the entirety of the posterior, not just plugging summary statistics from it into the priors of subsequent analyses. Correct? Apr 28, 2018 at 13:11
• @MarkWhite Correct. The posterior distributions from your first analysis should be your priors for the second. Apr 28, 2018 at 16:01
• @Kodiologist and summary statistics about the posterior != the posterior Apr 28, 2018 at 16:02
• @MarkWhite Right. Apr 28, 2018 at 16:03

First I should point out that:

1. In your significance-testing approach, you followed up a negative result with a different model that gave you another chance to get a positive result. Such a strategy increases your project-wise type-I error rate. Significance-testing requires choosing your analytic strategy in advance for the $p$-values to be correct.
2. You're putting a lot of faith in the results of Study 1 by translating your findings from that sample so directly into priors. Remember, a prior is not just a reflection of past findings. It needs to encode the entirety of your preexisting beliefs, including your beliefs before the earlier findings. If you admit that Study 1 involved sampling error as well as other kinds of less tractiable uncertainty, such as model uncertainty, you should be using a more conservative prior.

The second of these points to an important departure you have made from Bayesian convention. You didn't set a prior first and then fit both models in Bayesian fashion. You fit one model in a non-Bayesian fashion and then used that for priors for the other model. If you used the conventional approach, you wouldn't see the dependence on order that you saw here.

• 1. How did I follow up a negative result with a different model? What do you mean by "negative result"? As far as study-wide Type I error rate, these are two separate studies conducted weeks apart from one another. Either way, I believe in doing exploratory data analysis, so I don't ever think p-values in practice are "correct" or that we should expect them to be "totally correct." If people only did the tests they thought of beforehand, we would miss out on lots of great findings that happened by accident—and we'd be wasting tons of data. Apr 27, 2018 at 17:08
• 1. A negative result is one that is unexciting or disappointing, or more specifically in the context of significance testing, a negative result is failing to reject a null hypothesis. If you don't think that $p$-values are ever correct, of course, then significance-testing can't be of any value even in theory. There's nothing wrong with a exploratory philosophy, but significance-testing isn't suited for it. By "study-wise", I actually meant "project-wise", in the sense of the word "project" encompassing both studies; I've corrected that. Apr 27, 2018 at 18:28
• 2. Yes, but you would end up with different priors for Study 2, which didn't end up with putting so much credence into the idea that Study 1 was accurate. Apr 27, 2018 at 18:28
• 1. The problem isn't that you collected more data and analyzed it, but that you reanalyzed the data from both studies (with a unified model with a new predictor) because you got negative results the first time you analyzed the second dataset. I've never seen reason to believe that significance-testing is actually useful, but most of those who believe it is seem to think that all the theorems about significance-testing are what support its usefulness, and the theorems, like all theorems, require certain premises in order to get their conclusions. Apr 27, 2018 at 18:38
• @Kodiologist - If you don't think that significance testing is ever useful, on what basis are you suspicious of (for example) the researcher who concludes that most people likely have blue eyes because everyone in their sample of two did? Apr 27, 2018 at 22:37

I thought I might make a series of graphs with a different, but stylized problem, to show you why it can be dangerous to go from Frequentist to Bayesian methods and why using summary statistics can create issues.

Rather than use your example, which is multidimensional, I am going to cut it down to one dimension with two studies whose size is three observations and three observations.

The data I am using is fake. Both samples have been forced to have a median of -1. This matters because it is coming from a simplified density function that I have to commonly work with. The Frequentist density and the Bayesian Likelihood function is $$\frac{1}{\pi}\frac{1}{1+(x-\theta)^2}.$$ This is the Cauchy distribution with unknown median, but with a scale parameter of one. In truncated form, it is seen as the most common case in the stock market, and appears in physics problems with rotating objects such as rocks rolling downhill or in the famous "Gull's Lighthouse Problem."

I am using it because the central limit theorem doesn't apply, it lacks sufficient statistics, extreme observations are common, Chebychev's inequality doesn't hold and a whole host of normally workable solutions fall apart. I am using it because it makes for great examples without having to put too much work into the problem.

There are two samples. In the first study, the data was $\{-5,-1,4\}$. In the second study, the data was $\{-1.5,-1,-.5\}$. This distribution is nice because highly concentrated samples are common and samples with a massive range are common. The 99.99% confidence interval is normally $\pm{669}\sigma$ rather than the $\pm{3}\sigma$ most are used to.

The posterior densities of the two separate studies is

As is visually obvious, taking summary statistics from sample one could be incredibly misleading. If you are used to seeing nice, unimodal, well-defined and named densities, then that can quickly go out the door with Bayesian tools. There is no named distribution like it, but you could certainly describe it with summary statistics had you not visually looked at it. Using a summary statistic could be a problem if you are then going to use that to build a new prior.

The Frequentist confidence distribution for both samples are the same. Because the scale is known, the only unknown parameter is the median. For a sample size of three, the median is the MVUE. While the Cauchy distribution has no mean or variance, the sampling distribution of the median does. It is less efficient than the maximum likelihood estimator, but it takes me no effort to calculate. For large sample sizes Rothenberg's method is the MVUE and there are medium sample size solutions as well.

For the Frequentist distribution, you get

Notice that had you used summary statistics you would have gotten the same ones for both samples. The Frequentist distribution doesn't depend much on the data because the scale parameter is known and they have the same medians. So the summary statistics are invariant to the differences in the samples, because of the common median. While you would rightly point out that this is contrived and this wouldn't really happen, the distortion remains. Using language more correct for Bayesian thinking, the Frequentist model is $\Pr(x|\theta)$ rather than $\Pr(\theta|x)$.

The Frequentist distribution assumes an infinite repetition of sample size three draws and shows the limiting distribution for the distribution of sample medians. The Bayesian distribution is given $x$ so it depends only on the observed sample and ignores the good or bad properties that this sample may have. Indeed, the sample is unusual for Bayesian methods and so one may be given pause to form a strong inference about it. This is why the posterior is so wide, the sample is unusual. The Frequentist method is controlling for unusual samples, while the Bayesian is not. This creates the perverse case where the added certainty of the scale parameter narrows the Frequentist solution, but widens the Bayesian.

The joint posterior is the product of both posteriors and by associativity of multiplication, it does not matter which order you use. Visually, the joint posterior is .

It is obvious that had you imposed some simplified distribution on the posteriors and used their summary statistics, you would likely get a different answer. In fact, it could have been a very different answer. If a 70% credible region been used for study one, it would have resulted in a disconnected credible region. The existence of disconnected intervals happens in Bayesian methods sometimes. The graphic of the highest density interval and the lowest density interval for study one is

You will notice that the HDR is broken by a sliver of a region which is outside the credible set.

While many of these problems commonly disappear in large sets with regression, let me give you an example of a natural difference in how Bayesian and Frequentist methods will handle missing variables differently in regression.

Consider a well constructed regression with one missing variable, the weather. Let us assume that customers behave differently on rainy days and sunny days. If that difference is enough there can easily be two Bayesian posterior modes. One mode reflects the sunny behavior, the other the rainy. You don't know why you have two modes. It could be a statistical run or it could be a missing data point, but either your sample is unusual or your model has an omitted variable.

The Frequentist solution would average the two states and may put the regression line in a region where no customer behavior actually occurs, but which averages out the two types of behavior. It will also be downward biased. The issues may get caught in the analysis of residuals, particularly if there is a large difference in the true variances, but it may not. It may be one of those weird pictures of residuals that will show up on Cross-validated from time to time.

The fact you have two different posteriors from the same data implies that you didn't multiply the two together directly. Either you created a posterior from a Frequentist solution that didn't map one-to-one with the Bayesian posterior, or you created a prior from the summary statistics and the likelihood function wasn't perfectly symmetric, which is common.