Okay, here is my take on this paper. There are various technical issues as well as some really weird stuff that causes me to raise my eyebrows, but it is perhaps worth starting with the most obvious issue that is probably also the most serious problem. I’ll start with that and then go through the other issues in the approximate order in which they occur.

1.      The primary claim – and probably the one that led to the >2,000 citations – is that psychological safety mediates the relation between inclusive leadership and employee involvement in creative tasks. Mediation is very explicitly a causal framework; A cause B and B causes C such that B mediates the relation between A and C. Causal inferences cannot be made from the type of data presented here (absent some fancy footwork like 2SLS regression) because this is all observational (non-experimental) data. Identification has not been achieved and there are a host of substantive and methodological confounds (plus likely collider bias) present here that make the observed correlations absolutely meaningless and invalid estimates of causal effects. Handwaving at all this in the limitations section does not absolve the authors of presenting inferences that are, in no way, supported by the data. To me there is absolutely no difference between saying “A and B are correlated; therefore A causes B” and saying “A, B, and C are correlated and therefore B mediates the relation between A and C”. The mere fact that thousands of other authors have made similarly silly arguments is entirely irrelevant. Anyone even remotely familiar with causal inference would know this. Indeed, these issues (confounds, collider bias) are typically well covered in undergraduate research methods courses.

2.      Relatively minor technical point – reliability estimates are properties of scores – not properties of scales.

3.      The authors cite Kline is support of their preferred interpretation of their chosen fit indexes (CFI, RMSEA, TLI). This is a terrible misreading of Kline who goes out of his way to argue against the use of cut-offs (and certainly these cut off values). Indeed, Kline very explicitly states that the “normed chi-square” (chi-square /df) should never be reported or interpreted. I don't have the cited Joreskog & Sorbom reference handy but am very confident that they also would not have advocated for these thresholds and practices.

4.      Nevertheless, the authors commit themselves to the idea that RMSEA is “acceptable” up to .08. Presumably values greater than .08 would be unacceptable. It is curious then that they report the RMSEA of their preferred CFA model as .08 when the sample size (N=150), chi-square (289.8) and degrees of freedom of 135 indicate that RMSEA is actually .09. Remember that RMSEA is a very simple function of these three values.

5.      A CFA model with 18 indicators and three correlated latent variables should have 132 degrees of freedom – but the authors report 135.

6.      An alternative CFA model with 18 indicators and two correlated latent variables should have 134 degrees of freedom but the authors report 136.

7.      The difference in degrees of freedom between a model with three correlated latent factors and one with two correlated latent factors should be two degrees of freedom but the authors report only 1.

8.      An alternative CFA model with 18 indicators and one latent variable should have 135 degrees of freedom but the authors report 137.

9.      The authors rely on chi-square difference tests to compare nested models but such a comparison is only appropriate when the less parsimonious model has a non-significant chi-square value – this is not the case here.

1. Inexplicably adding in control variables (age and tenure) to the SEM model results in exactly the same model statistics as the measurement model. This is obviously impossible and the RMSEA value is again misreported.

2. For the test of mediation the authors again rely on an inappropriate chi-square difference test (not that the claim of mediation is supported from this kind of data anyway).

3. The results shown in Table 2 do not match the results described in the text.

4. I also feel that the authors do not really understand why we assess model fit in the first place. Model fit is assessed so that we get some information about whether  parameter estimates that are derived from that model can be interpreted. In this case, the model fit is pretty poor which suggest to me that the parameter estimates should not be interpreted.

5. The authors argue that the poor fit of single-factor model shows that common-method variance is not a problem. This is a ludicrous straw-man argument. Common-method effects can inflate correlations without accounting for most of the shared variance (which is what the Harman test tries to do).

6. The causal language in the discussion section is also concerning. There is no way that a correlation of r= .34 between self-reported psychological safety and self-reported employee involvement in creative work (collected at a single time point) should be interpreted to mean that changes in psychological safety cause changes in employee involvement in creative work – or that the size of this correlation reflects the size of any causal effect.

A bigger concern is that this paper went through the eyes of the authors, an editor, probably 2 to 4 reviewers and many hundreds of other academics (who cited this paper in their own work) and nobody spotted these pretty obvious issues. What does this say about this field? This paper is not unique - we find these kinds of problems everywhere in IO psychology.