I'm not sure I would say I'm an expert in information geometry, I worked for several years as a postdoc in a lab that focuses on the subject. As a disclaimer, this is entirely my own opinion and others may disagree.

Since you asked this question, the research situation in the field has improved. Firstly, two separate books ([1$ $], [2$ $]) have been published, both of which are good references for the material. In particular, the second gives a rigorous mathematical treatment for the basic theory. Secondly, a new journal, Information Geometry, has been released. Thus far several issues have been published and they contain some interesting papers.

However, information geometry is definitely a relatively niche mathematical field. As to the reason for this, in my opinion IG is really an interdisciplinary field and not simply a branch of mathematics. Many of the people working in the field are not mathematicians by background. As a result, information geometry embodies a wide range of research. Some papers are mathematical, but many others are really statistics, computer science, or some hybrid thereof. Many of the publishing conventions are differ from math, as well. For instance, it's common to publish short papers without proofs in conference proceedings and, generally speaking, the main theorems are not stated in the introduction.

While there is a lot of good work being done in the field, there is also too much research that is not really serious. Most of this is not done in bad faith, but seems due to a lack of experience and background in geometry. Furthermore, a lot of the work is published in a for-profit journal whose peer review process is quite suspect. Without giving examples, some papers boil down to slightly modifying known results and treating them as novel. Other papers try to use really big ideas without understanding the underlying theory or really proving anything. Furthermore, what is considered acceptable overlap between publications is far greater than in pure math. Needless to say, this creates serious problems for the field, and makes it much less likely to be taken seriously.

Even with the good papers, they often seem to lack a good punchline. As was mentioned in the comments, the math in IG has built up a very general foundational theory, often without providing mathematical motivation for this theory. My impression is that quite a few of the researchers in the field were heavily influenced by the "structural point of view" pioneered by Nomizu and Kobayashi. I suppose the motivation for these structures might be self-evident to a statistician, but as a geometer oftentimes it's completely lost on me. In my experience, I only really started to understand what was going on when I worked through some important examples of statistical manifolds, instead of trying to learn the theory from the ground up.

Related to the point above, it's difficult to find explicit conjectures in the field. There isn't something similar to Yau's list of open problems in geometry to guide progress in the field. As such, when I was learning the field it was hard to tell what was considered an important problem and to understand the motivations for the research.

As a result of all of these factors, information geometry has remained a specialized sub-field. I think this will remain the case unless it is used to solve a big problem or it evolves to be more in line with standard mathematical conventions. All that being said, I've learned a lot from information geometry, and there is definitely a fair amount of relatively low-hanging fruit to be picked. Furthermore, the field seems to be making progress in recent years, so hopefully my critiques will soon be obsolete.

To end on a positive note, let me give an example of a paper that I think does things well [3$ $]. This work studies necessary conditions for a Riemannian manifold to locally be written as the Hessian of a convex potential. I really like this paper and have found it helpful for my intuition.

P.S. If anyone is interested, I was able to find a list of open problems from 1998, some of which have since been solved.

**References**

[1$ $] Amari, S. I. (2016). Information geometry and its applications (Vol. 194). Tokyo: Springer.

[2$ $] Ay, N., Jost, J., Vân Lê, H., & Schwachhöfer, L. (2017). Information geometry (Vol. 8). Berlin: Springer.

[3$ $] Amari, S. I., & Armstrong, J. (2014). Curvature of Hessian manifolds. Differential Geometry and its Applications, 33, 1-12.