While I wouldn't call myself an expert in information geometry, I am a postdoc in a lab that focuses on the subject. My background is in geometric analysis, but I started working on IG a year ago. 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 two issues have been published and they both contain some interesting papers.
However, information geometry is definitely a relatively niche mathematical field. Personally, I prefer things this way; information geometry gives a rich class of examples and there is relatively low-hanging fruit to be found.
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. It's not done in bad faith, but seems due to a lack of experience and background in geometry. 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.
Even with the good papers, they often seem to lack a good punchline. The math in IG has built up a very general foundational theory, often without providing mathematical motivation for this theory. I suppose the motivation might be self-evident for a statistician, but as a geometer oftentimes it's completely lost on me. Furthermore, it's difficult to find explicit conjectures in the field. Unfortunately, there isn't something similar to Yau's list of open problems in geometry to guide progress in the field.
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 I think it's definitely worthwhile for the working geometer to know some of the basic examples. Furthermore, the field seems to be making good 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$ $]. This work studies necessary conditions for a Riemannian manifold to locally be written as the Hessian of a convex potential. I really like this paper and have found it helpful for my intuition.
P.S. If anyone is interested, I was able to find a list of open problems from 1998, some of which have since been solved. In quantum information geometry, another open question is the Petz conjecture. This states that the scalar curvature of the Kubo-Mori metric is monotonic under stochastic processes. There is some work  which reduces the conjecture to a few seemingly elementary, yet extremely tricky, inequalities. If you are interested in this problem, feel free to shoot me an e-mail.
[1$ $] Amari, S. I. (2016). Information geometry and its applications (Vol. 194). Tokyo: Springer.
[2$ $] Ay, N., Jost, J., Vân Lê, H., & Schwachhöfer, L. (2017). Information geometry (Vol. 8). Berlin: Springer.
[3$ $] Amari, S. I., & Armstrong, J. (2014). Curvature of Hessian manifolds. Differential Geometry and its Applications, 33, 1-12.
 Andai, A. (2003). On the monotonicity conjecture for the curvature of the Kubo-Mori metric. arXiv preprint math-ph/0310064.